Reviewer #3 (Public review):

Summary:

The authors aimed to investigate the multifaceted roles of the Inferior Colliculus (IC) in auditory and cognitive processes in monkeys. Through extracellular recordings during a sound duration-based novelty detection task, the authors observed a "climbing effect" in neuronal firing rates, suggesting an enhanced response during sensory prediction. Observations of reward prediction errors within the IC further highlight its complex integration in both auditory and reward processing. Additionally, the study indicated IC neuronal activities could be involved in decision-making processes.

Strengths:

This study has the potential to significantly impact the field by challenging the traditional view of the IC as merely an auditory relay station and proposing a more integrative role in cognitive processing. The results provide valuable insights into the complex roles of the IC, particularly in sensory and cognitive integration, and could inspire further research into the cognitive functions of the IC.

Weaknesses:

Major Comments:

(1) Structural Clarity and Logic Flow:<br /> The manuscript investigates three intriguing functions of IC neurons: sensory prediction, reward prediction, and cognitive decision-making, each of which is a compelling topic. However, the logical flow of the manuscript is not clearly presented and needs to be well recognized. For instance, Figure 3 should be merged into Figure 2 to present population responses to the order of sounds, thereby focusing on sensory prediction. Given the current arrangement of results and figures, the title could be more aptly phrased as "Beyond Auditory Relay: Dissecting the Inferior Colliculus's Role in Sensory Prediction, Reward Prediction, and Cognitive Decision-Making."

(2) Clarification of Data Analysis:<br /> Key information regarding data analysis is dispersed throughout the results section, which can lead to confusion. Providing a more detailed and cohesive explanation of the experimental design would significantly enhance the interpretation of the findings. For instance, including a detailed timeline and reward information for the behavioral paradigms shown in Figures 1C and D would offer crucial context for the study. More importantly, clearly presenting the analysis temporal windows and providing comprehensive statistical analysis details would greatly improve reader comprehension.

(3) Reward Prediction Analysis:<br /> The conclusion regarding the IC's role in reward prediction is underdeveloped. While the manuscript presents evidence that IC neurons can encode reward prediction, this is only demonstrated with two example neurons in Figure 6. A more comprehensive analysis of the relationship between IC neuronal activity and reward prediction is necessary. Providing population-level data would significantly strengthen the findings concerning the IC's complex functionalities. Additionally, the discussion of reward prediction in lines 437-445, which describes IC neuron responses in control experiments, does not sufficiently demonstrate that IC neurons can encode reward expectations. It would be valuable to include the responses of IC neurons during trials with incorrect key presses or no key presses to better illustrate this point.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This work made a lot of efforts to explore the multifaceted roles of the inferior colliculus (IC) in auditory processing, extending beyond traditional sensory encoding. The authors recorded neuronal activitity from the IC at single unit level when monkeys were passively exposed or actively engaged in behavioral task. They concluded that 1）IC neurons showed sustained firing patterns related to sound duration, indicating their roles in temporal perception, 2) IC neuronal firing rates increased as sound sequences progress, reflecting modulation by behavioral context rather than reward anticipation, 3) IC neurons encode reward prediction error and their capability of adjusting responses based on reward predictability, 4) IC neural activity correlates with decision-making. In summary, this study tried to provide a new perspective on IC functions by exploring its roles in sensory prediction and reward processing, which are not traditionally associated with this structure.

Strengths:

The major strength of this work is that the authors performed electrophysiological recordings from the IC of behaving monkeys. Compared with the auditory cortex and thalamus, the IC in monkeys has not been adequately explored.

We appreciate the reviewer’s acknowledgment of the efforts and strengths of our study. Indeed, our goal was to provide a comprehensive exploration of the multifaceted roles of the inferior colliculus (IC) in auditory processing and beyond, particularly in sensory prediction and reward processing. The use of electrophysiological recordings in behaving monkeys was central to our approach, as we sought to uncover the underexplored aspects of IC function in these complex cognitive domains. We are pleased that the reviewer recognizes the value of investigating the IC, a structure that has not been adequately explored in primates compared to other auditory regions like the cortex and thalamus. This feedback reinforces our belief that our work contributes significantly to advancing the understanding of the IC's roles in cognitive processing.

We look forward to addressing any further points the reviewers may have and refining our manuscript accordingly. Thank you for your constructive feedback and for recognizing the strengths of our research approach.

Weaknesses:

(1) The authors cited several papers focusing on dopaminergic inputs in the IC to suggest the involvement of this brain region in cognitive functions. However, all those cited work were done in rodents. Whether monkey's IC shares similar inputs is not clear.

We appreciate the reviewer's insightful comment on the limitations of extrapolating findings from rodent models to monkeys, particularly concerning dopaminergic inputs to the Inferior Colliculus (IC). While it is true that most studies on dopaminergic inputs to the IC have been conducted in rodents, to our knowledge, no studies have been conducted specifically in primates. To address the reviewer's concern, we have added a statement in both the introduction and discussion sections of our manuscript:

- Introduction: " However, these studies were conducted in rodents, and the existence and role of dopaminergic inputs in the primate IC remain underexplored."

- Discussion: " However, the exact mechanisms and functions of dopamine modulation in the inferior colliculus are still not fully understood, particularly in primates. "

(2) The authors confused the two terms, novelty and deviation. According to their behavioral paradigm, deviation rather than novelty should be used in the paper because all the stimuli have been presented to the monkeys during training. Therefore, there is actually no novel stimuli but only deviant stimuli. This reflects that the author has misunderstood the basic concept.

We appreciate the reviewer's clarification regarding the distinction between "novelty" and "deviation" in the context of our behavioral paradigm. We agree that, given the nature of our experimental design where all stimuli were familiar to the monkeys during training, the term "deviation" more accurately describes the stimuli used in our study rather than "novelty."

To address this, we have revised the manuscript to replace the term "novelty" with "deviation" wherever applicable. This change has been made to ensure accurate terminology is used throughout the paper, thereby eliminating any potential misunderstanding of the concepts involved in our study.

We thank the reviewer for pointing out this important distinction, which has improved the clarity and precision of our manuscript.

(3) Most of the conclusions were made based on correlational analysis or speculation without providing causal evidences.

We appreciate the reviewer’s concern regarding the reliance on correlational analyses in our study. Indeed, we acknowledge that the conclusions drawn primarily reflect correlations between neuronal activity and behavioral outcomes, rather than direct causal evidence. This limitation is inherent to many electrophysiological studies, particularly those conducted in behaving primates, where direct manipulation of specific neural circuits to establish causality is often challenging.

This limitation becomes even more complex when considering the IC’s role as a key lower-level relay station in the auditory pathway. Manipulating IC activity could potentially affect auditory responses in downstream pathways, which, in turn, may influence sensory prediction and decision-making processes. Moreover, we hypothesize that the sensory prediction and reward signals observed in the IC may not have direct causal effects but may instead be driven by top-down projections from higher cognitive regions. However, it is important to emphasize that our study provides novel evidence that the IC may exhibit multiple facets of cognitive signaling, which could inspire future research into the underlying mechanisms and broader functional implications of these signals.

To address this, we have taken the following steps in our revised manuscript:

(1) Clarified the Scope of Conclusions: We have revised the language in the Results and Discussion sections to explicitly state that our findings represent correlational relationships rather than causal mechanisms. For example, we now refer to the associations observed between IC activity and behavioral outcomes as "correlational" and have refrained from making definitive causal claims without supporting experimental evidence.

(2) Proposed Future Directions: In the Discussion section, we have included suggestions for future studies to directly test the causality of the observed relationships. We acknowledge the need for further investigation to substantiate the causal links between IC activity and cognitive functions such as sensory prediction, decision-making, and reward processing.

We believe these revisions provide a more balanced interpretation of our findings while emphasizing the importance of future research to build on our results and establish causal relationships. Thank you for raising this critical point, which has led to a more rigorous and transparent presentation of our study.

(4) Results are presented in a very "straightforward" manner with too many detailed descriptions of phenomena but lack of summary and information synthesis. For example, the first section of Results is very long but did not convey clear information.

We appreciate the reviewer’s feedback regarding the presentation of our results. We understand that the detailed descriptions of phenomena may have made it difficult to discern the key findings and overarching themes in the study. We recognize the importance of balancing detailed reporting with clear summaries and synthesis to effectively communicate our findings.

To address this concern, we have made the following revisions to the manuscript:

(1) Condensed and Synthesized Key Findings: We have streamlined the presentation of the Results section by condensing overly detailed descriptions and focusing on the most critical aspects of the data. Key findings are now summarized at the end of each subsection to ensure that the main points are clearly conveyed.

(2) Enhanced Section Summaries: We have added summary statements at the end of each major results section to synthesize the findings and highlight their significance. This should help guide the reader through the narrative and emphasize the key takeaways from each part of the study.

(3) Improved Flow and Clarity: We have revised the structure and organization of the Results section to improve the flow of information. By rearranging certain paragraphs and refining the language, we aim to present the results in a more cohesive and coherent manner.

We believe these changes will make the Results section more accessible and informative, allowing readers to more easily grasp the significance of our findings. Thank you for your valuable suggestion, which has significantly improved the clarity and impact of our manuscript.

(5) The logic between different sections of Results is not clear.

We appreciate the reviewer’s observation regarding the lack of clear logical connections between different sections of the Results. We acknowledge that a coherent flow is essential for effectively communicating the progression of findings and their implications.

To address this concern, we have made the following revisions:

(1) Enhanced Transitions Between Sections: We have introduced clearer transitional statements between sections of the Results. These transitions explicitly state how each new section builds upon or relates to the previous findings, creating a more cohesive narrative.

(2) Integration of Findings: In several places within the Results, we have added brief synthesis paragraphs that integrate findings across sections. These integrative summaries help to tie together the different aspects of our study, demonstrating how they collectively contribute to our understanding of the Inferior Colliculus’s (IC) role in sensory prediction, decision-making, and reward processing.

(3) Clarified Rationale: At the beginning of each major section, we have clarified the rationale behind why certain experiments were conducted, connecting them more clearly to the overarching goals of the study. This should help the reader understand the purpose of each set of results in the context of the broader research objectives.

We believe these changes improve the overall coherence and readability of the Results section, allowing readers to better follow the logical progression of our study. We are grateful for this constructive feedback and believe it has significantly enhanced the manuscript.

(6) In the Discussion, there is excessive repetition of results, and further comparison with and discussion of potentially related work are very insufficient. For example, Metzger, R.R., et al. (J Neurosc, 2006) have shown similar firing patterns of IC neurons and correlated their findings with reward.

We appreciate the reviewer's insightful critique regarding the excessive repetition in the Discussion and the lack of sufficient comparison with related work. We acknowledge that a well-balanced Discussion should not only interpret findings but also place them in the context of existing literature to highlight the novelty and significance of the study.

To address these concerns, we have made the following revisions:

(1) Reduction of Repetition: We have carefully revised the Discussion to minimize redundant repetition of the Results. Instead of restating the findings, we now focus more on their implications, limitations, and how they advance the current understanding of the Inferior Colliculus (IC) and its broader cognitive roles.

(2) Incorporation of Related Work: We have expanded the Discussion to include a more comprehensive comparison with existing literature, specifically highlighting studies that have reported similar findings. For example, we now discuss the work by Metzger et al. (2006), which demonstrated similar firing patterns of IC neurons and correlated these with reward-related processes. This comparison helps contextualize our results and emphasizes the novel contributions our study makes to the field.

We believe these revisions have significantly improved the quality of the Discussion by reducing unnecessary repetition and providing a more thorough engagement with the relevant literature. We are grateful for the reviewer's valuable feedback, which has helped us refine and strengthen the manuscript.

Reviewer #2 (Public review):

Summary:

The inferior colliculus (IC) has been explored for its possible functions in behavioral tasks and has been suggested to play more important roles rather than simple sensory transmission. The authors revealed the climbing effect of neurons in IC during decision-making tasks, and tried to explore the reward effect in this condition.

Strengths:

Complex cognitive behaviors can be regarded as simple ideals of generating output based on information input, which depends on all kinds of input from sensory systems. The auditory system has hierarchic structures no less complex than those areas in charge of complex functions. Meanwhile, IC receives projections from higher areas, such as auditory cortex, which implies IC is involved in complex behaviors. Experiments in behavioral monkeys are always time-consuming works with hardship, and this will offer more approximate knowledge of how the human brain works.

We greatly appreciate the reviewer's positive summary of our work and recognition of the effort involved in conducting experiments on behaving monkeys. We agree with the reviewer that the inferior colliculus (IC) plays a significant role beyond mere sensory transmission, particularly in integrating sensory inputs with higher cognitive functions. Our study aims to shed light on these complex functions by revealing the climbing effect of IC neurons during decision-making tasks and exploring how reward influences this dynamic.

We are encouraged that the reviewer acknowledges the importance of investigating the IC's role within the broader framework of complex cognitive behaviors and appreciates the hierarchical nature of the auditory system. The reviewer's comments reinforce the value of our research in contributing to a more nuanced understanding of how the IC might contribute to sensory-cognitive integration.

We thank the reviewer for highlighting the significance of using behavioral monkey models to approximate human brain function. We are hopeful that our findings will serve as a stepping stone for further research exploring the multifaceted roles of the IC in cognition and behavior.

We will now proceed to address the specific concerns and suggestions provided by the reviewer in the following sections.

Weaknesses:

These findings are more about correlation but not causality of IC function in behaviors. And I have a few major concerns.

We appreciate the reviewer’s concern regarding the reliance on correlational analyses in our study. We acknowledge the importance of distinguishing between correlation and causality. As detailed in our response to Question 3 from Reviewer #1, we recognize the limitations of relying on correlational data and the challenges of establishing direct causal links in electrophysiological studies involving behaving primates.

We have taken steps to clarify this distinction throughout our manuscript. Specifically, we have revised the Results and Discussion sections to ensure that the findings are presented as correlational, not causal, and we have proposed future studies utilizing more direct manipulation techniques to assess causality. We hope these revisions adequately address your concerns.

Comparing neurons' spike activities in different tests, a 'climbing effect' was found in the oddball paradigm. The effect is clearly related to training and learning process, but it still requires more exploration to rule out a few explanations. First, repeated white noise bursts with fixed inter-stimulus-interval of 0.6 seconds was presented, so that monkeys might remember the sounds by rhymes, which is some sort of learned auditory response. It is interesting to know monkeys' responses and neurons' activities if the inter-stimuli-interval is variable. Second, the task only asked monkeys to press one button and the reward ratio (the ratio of correct response trials) was around 78% (based on the number from Line 302). so that, in the sessions with reward, monkeys had highly expected reward chances, does this expectation cause the climbing effect?

We thank the reviewer for raising these insightful points regarding the 'climbing effect' observed in the oddball paradigm and its potential relationship with training, learning processes, and reward expectation. Below, we address each of the reviewer's specific concerns:

(1) Inter-Stimulus Interval (ISI) and Rhythmic Auditory Response:

The reviewer suggests that the fixed inter-stimulus interval (ISI) of 0.6 seconds might lead to a rhythmic auditory response, where monkeys could anticipate the sounds. We appreciate this perspective. However, we believe that rhythm is unlikely to play a significant role in the 'climbing effect' for the following reason: The 'climbing effect' starts from the second sound in the block (Fig.2D and Fig.3B), before any rhythm or pattern could be fully established, as a rhythm generally requires at least three repetitions to form. Unfortunately, we did not explore variable ISIs in the current study, so we cannot directly address this concern with the data at hand.

(2) Reward Expectation and Climbing Effect:

The reviewer raises an important concern about whether the 'climbing effect' could be influenced by the monkeys' high reward expectation, especially given the high reward ratio (~78%) in the sessions. While it is plausible that reward expectation could contribute to the observed increase in neuronal firing rates, we believe the results from our reward experiment (Fig. 4) suggest otherwise. In this experiment, even though reward expectation was likely formed due to the consistent pairing of sounds with rewards (100%), we did not observe a climbing effect in the auditory response. The presence of reward prediction error (Fig. 4D) further suggests that while the monkeys may form reward expectations, these expectations do not directly drive the climbing effect.

To clarify this point, we have added sentences in the revised manuscript to explicitly discuss the relationship between reward expectation and the climbing effect, emphasizing that our findings indicate the climbing effect is not primarily due to reward expectation.

We believe these revisions provide a clearer understanding of the factors contributing to the climbing effect and address the reviewer's concerns effectively. Thank you for these valuable suggestions.

"Reward effect" on IC neurons' responses were showed in Fig. 4. Is this auditory response caused by physical reward action or not? In reward sessions, IC neurons have obvious response related to the onset of water reward. The electromagnetic valve is often used in water-rewarding system and will give out a loud click sound every time when the reward is triggered. IC neurons' responses may be simply caused by the click sound if the electromagnetic valve is used. It is important to find a way to rule out this simple possibility.

We appreciate the reviewer’s concern regarding the potential confounding factor introduced by the electromagnetic valve’s click sound during water reward delivery, which could be misinterpreted as an auditory response rather than a response to the reward itself. Anticipating this possibility, we took measures to eliminate it by placing the electromagnetic valve outside the soundproof room where the neuronal recordings were performed.

To address your concern more explicitly, we have added sentences in the Methods section of the revised manuscript detailing this setup, ensuring that readers are aware of the steps we took to eliminate this potential confound. By doing so, we believe that the observed reward-related neural activity in the IC is attributable to the reward processing itself rather than an auditory response to the valve click. We appreciate you bringing this important aspect to our attention, and we hope our clarification strengthens the interpretation of our findings.

Reviewer #3 (Public review):

Summary:

The authors aimed to investigate the multifaceted roles of the Inferior Colliculus (IC) in auditory and cognitive processes in monkeys. Through extracellular recordings during a sound duration-based novelty detection task, the authors observed a "climbing effect" in neuronal firing rates, suggesting an enhanced response during sensory prediction. Observations of reward prediction errors within the IC further highlight its complex integration in both auditory and reward processing. Additionally, the study indicated IC neuronal activities could be involved in decision-making processes.

Strengths:

This study has the potential to significantly impact the field by challenging the traditional view of the IC as merely an auditory relay station and proposing a more integrative role in cognitive processing. The results provide valuable insights into the complex roles of the IC, particularly in sensory and cognitive integration, and could inspire further research into the cognitive functions of the IC.

We appreciate the reviewer’s positive summary of our work and recognition of its potential impact on the field. We are pleased that the reviewer acknowledges the significance of our findings in challenging the traditional view of the Inferior Colliculus (IC) as merely an auditory relay station and in proposing its integrative role in cognitive processing.

Our study indeed aims to provide new insights into the multifaceted roles of the IC, particularly in the context of sensory and cognitive integration. We believe that this research could pave the way for future studies that further explore the cognitive functions of the IC and its involvement in complex behavioral processes.

We are encouraged by the reviewer’s positive assessment and are committed to continuing to refine our work in response to the constructive feedback provided. We hope that our findings will contribute to advancing the understanding of the IC’s role in the broader context of neuroscience.

We will now proceed to address the specific concerns and suggestions provided by the reviewer in the following sections.

Weaknesses:

Major Comments:

(1) Structural Clarity and Logic Flow:

The manuscript investigates three intriguing functions of IC neurons: sensory prediction, reward prediction, and cognitive decision-making, each of which is a compelling topic. However, the logical flow of the manuscript is not clearly presented and needs to be well recognized. For instance, Figure 3 should be merged into Figure 2 to present population responses to the order of sounds, thereby focusing on sensory prediction. Given the current arrangement of results and figures, the title could be more aptly phrased as "Beyond Auditory Relay: Dissecting the Inferior Colliculus's Role in Sensory Prediction, Reward Prediction, and Cognitive Decision-Making."

We appreciate the reviewer’s detailed feedback on the structural clarity and logical flow of the manuscript. We understand the importance of presenting our findings in a clear and cohesive manner, especially when addressing multiple complex topics such as sensory prediction, reward prediction, and cognitive decision-making.

To address the reviewer's concerns, we have made the following revisions:

(1) Reorganization of Figures and Results:

We agree with the suggestion to merge Figure 3 into Figure 2. By doing so, we can present the population responses to the order of sounds more effectively, thereby streamlining the focus on sensory prediction. This will allow readers to more easily follow the progression of the results related to this key function of the IC.

We have reorganized the Results section to ensure a smoother transition between the different aspects of IC function that we are investigating. The new structure will better guide the reader through the narrative, aligning with the themes of sensory prediction, reward prediction, and cognitive decision-making.

(2) Revised Title:

In line with the reviewer's suggestion, we have revised the title to "Beyond Auditory Relay: Dissecting the Inferior Colliculus's Role in Sensory Prediction, Reward Prediction, and Cognitive Decision-Making." We believe this title more accurately reflects the scope and focus of our study, as it highlights the three core functions of the IC that we are investigating.

(3) Improved Logic Flow:

We have added introductory statements at the beginning of each section within the Results to clarify the rationale behind the experiments and the logical connections between them. This should help to improve the overall flow of the manuscript and make the progression of our findings more intuitive for readers.

We believe these changes significantly enhance the clarity and logical structure of the manuscript, making it easier for readers to understand the sequence and importance of our findings. Thank you for your valuable suggestion, which has led to a more coherent and focused presentation of our work.

(2) Clarification of Data Analysis:

Key information regarding data analysis is dispersed throughout the results section, which can lead to confusion. Providing a more detailed and cohesive explanation of the experimental design would significantly enhance the interpretation of the findings. For instance, including a detailed timeline and reward information for the behavioral paradigms shown in Figures 1C and D would offer crucial context for the study. More importantly, clearly presenting the analysis temporal windows and providing comprehensive statistical analysis details would greatly improve reader comprehension.

We appreciate the reviewer’s insightful comment regarding the need for clearer and more cohesive explanations of the data analysis and experimental design. We recognize that a well-structured presentation of this information is essential for the reader to fully understand and interpret our findings. To address this, we have made the following revisions:

(1) Detailed Explanation of Experimental Design:

We have included a more detailed explanation of the experimental design, particularly for the behavioral paradigms shown in Figures 1C and 1D. This includes a comprehensive timeline of the experiments, along with explicit information about the reward structure and timing. By providing this context upfront, we aim to give readers a clearer understanding of the conditions under which the neuronal recordings were obtained.

(2) Cohesive Presentation of Data Analysis:

Key information regarding data analysis, which was previously dispersed throughout the Results section, has been consolidated and moved to a dedicated subsection within the Methods. This subsection now provides a step-by-step description of the analysis process, including the temporal windows used for examining neuronal activity, as well as the specific statistical methods employed.

We have also ensured that the temporal windows used for different analyses (e.g., onset window, late window, etc.) are clearly defined and consistently referenced throughout the manuscript. This will help readers track the use of these windows across different figures and analyses.

(3) Enhanced Statistical Analysis Details:

We have expanded the description of the statistical analyses performed in the study, including the rationale behind the choice of tests, the criteria for significance, and any corrections for multiple comparisons. These details are now presented in a clear and accessible format within the Methods section, with relevant information also highlighted in the Result section or the figure legends to facilitate understanding.

We believe these changes will significantly improve the clarity and comprehensibility of the manuscript, allowing readers to better follow the experimental design, data analysis, and the conclusions drawn from our findings. Thank you for this valuable feedback, which has helped us to enhance the rigor and transparency of our presentation.

(3) Reward Prediction Analysis:

The conclusion regarding the IC's role in reward prediction is underdeveloped. While the manuscript presents evidence that IC neurons can encode reward prediction, this is only demonstrated with two example neurons in Figure 6. A more comprehensive analysis of the relationship between IC neuronal activity and reward prediction is necessary. Providing population-level data would significantly strengthen the findings concerning the IC's complex functionalities. Additionally, the discussion of reward prediction in lines 437-445, which describes IC neuron responses in control experiments, does not sufficiently demonstrate that IC neurons can encode reward expectations. It would be valuable to include the responses of IC neurons during trials with incorrect key presses or no key presses to better illustrate this point.

We deeply appreciate the detailed feedback provided regarding the conclusions on the inferior colliculus (IC)'s role in reward prediction within our manuscript. We acknowledge the importance of a robust and comprehensive presentation of our findings, particularly when discussing complex neural functionalities.

In response to the reviewers' concerns, we have made the following revisions to strengthen our manuscript:

(1) Inclusion of Population-Level Data for IC Neurons:

In the revised manuscript, we have included population-level results for IC neurons in a supplementary figure. Initially, we focused on two example neurons that did not exhibit motor-related responses to key presses to isolate reward-related signals. However, most IC neurons exhibit motor responses during key presses (as indicated in Fig.7), which can complicate distinguishing between reward-related activity and motor responses. This complexity is why we initially presented neurons without motor responses. To clarify this point, we have added sentences in the Results section to explain the rationale behind our selection of neurons and to address the potential overlap between motor and reward responses in the IC.

(2) Addition of Data on Key Press Errors and No-Response Trials:

In response to the reviewer’s suggestion, we have demonstrated Peri-Stimulus Time Histograms (PSTHs) for two example neurons during error trials as below, including incorrect key presses and no-response trials. Given that the monkeys performed the task with high accuracy, the number of error trials is relatively small, especially for the control condition (as shown in the top row of the figure). While we remain cautious in drawing definitive conclusions from this limited trials, we observed that no clear reward signals were detected during the corresponding window (typically centered around 150 ms after the end of the sound). It is important to note that the experiment was initially designed to explore decision-making signals in the IC, rather than focusing specifically on reward processing. However, the data in Fig. 6 demonstrated intriguing signals of reward prediction error, which is why we believe it is important to present them.

When combined with the results from our reward experiment (Fig. 5), we believe these findings provide compelling evidence of reward prediction errors being processed by IC neurons. Additionally, we observed that the reward prediction error in the IC appears to be signed, meaning that IC neurons showed robust responses to unexpected rewards but not to unexpected no-reward scenarios. However, the sign of the reward prediction error should be explored in greater depth with specifically designed experiments in future studies.

Author response image 1.

(A) PSTH of the neuron from Figure 6a during a key press trial under control condition. The number in the parentheses in the legend represents the number of trials for control condition. (B) PSTHs of the neuron from Figure 6a during non-key press trials under experimental conditions. The numbers in the parentheses in the legend represent the number of trials for experimental conditions. (C-D) Equivalent PSTHs as in A-B but from the neuron in Figure 6b.

We are grateful for the reviewer's insightful suggestions, which have allowed us to improve the depth and rigor of our analysis. We believe these revisions significantly enhance our manuscript's conclusions regarding the complex functionalities of IC.

eLife assessment

In this report, the authors present valuable findings identifying a novel worm-specific protein (sdg-1) that is induced upon loss of dsRNA import via SID-1, but is not required to mediate SID-1 RNA regulatory effects. The genetic and genomic approaches are well-executed. The existing data are solid, but the study would benefit from additional supporting evidence. The manuscript's central findings could also be refined to avoid overstating the results. These findings will be of interest to those working in the germline epigenetic inheritance field.

Reviewer #1 (Public review):

Summary:

In the manuscript "Intergenerational transport of double-stranded RNA limits heritable epigenetic changes" Shugarts and colleagues investigate intergenerational dsRNA transport in the nematode C. elegans. They induce oxidative damage in worms, blocking dsRNA import into cells (and potentially affecting the worms in other ways). Oxidative stress inhibits dsRNA import and the associated heritable regulation of gene expression in the adult germline (Fig. 2). The authors identify a novel gene, sid-1-dependent gene-1 (sdg-1), which is induced upon inhibition of SID-1 (Fig. 3). Both transient inhibition and genetic depletion of SID-1 lead to the upregulation of sdg-1 and a second gene, sdg-2 (Fig. 5). The expression of SDG-1 is variable, potentially indicating buffering regulation. While the expression of Sdg-1 could be consistent with a role in intergenerational transport of dsRNA, neither its overexpression nor loss-of-function impacts dsRNA-mediated silencing (Fig. 7) in the germline. It would be interesting to test if sdg-2 functions redundantly.

In summary, the authors have identified a novel worm-specific protein (sdg-1) that is induced upon loss of dsRNA import via SID-1, but is not required to mediate SID-1 RNA regulatory effects.

Remaining Questions:

• The authors use an experimental system that induces oxidative damage specifically in neurons to release dsRNAs into the circulation. Would the same effect be observed if oxidative damage were induced in other cell types?

• Besides dsRNA, which other RNAs and cellular products (macromolecules and small signalling molecules) are released into the circulation that could affect the observed changes in germ cells?

• SID-1 modifies RNA regulation within the germline (Fig. 7) and upregulates sdg-1 and sdg-2 (Fig. 5). However, SID-1's effects do not appear to be mediated via sdg-1. Testing the role of sdg-2 would be intriguing.

• Are sdg-1 or sdg-2 conserved in other nematodes or potentially in other species? Sdg-1 appears to be encoded or captured by a retro-element in the C. elegans genome and exhibits stochastic expression in different isolates. Is this a recent adaptation in the C. elegans genome, or is it present in other nematodes? Does loss-of-function of sdg-1 or sdg-2 have any observable effect?

Clarification for Readability:

To enhance readability and avoid misunderstandings, it is crucial to specify the model organism and its specific dsRNA pathways that are not conserved in vertebrates:

• In the first sentence of the paragraph "Here, we dissect the intergenerational transport of extracellular dsRNA ...", the authors should specify "in the nematode C. elegans". Unlike vertebrates, which recognise dsRNA as a foreign threat, worms and other invertebrates pervasively use dsRNA for signalling. Additionally, worms, unlike vertebrates and insects, encode RNA-dependent RNA polymerases that generate dsRNA from ssRNA substrates, enabling amplification of small RNA production. Especially in dsRNA biology, specifying the model organism is essential to avoid confusion about potential effects in humans.

• Similarly, the authors should specify "in C. elegans" in the sentence "Therefore, we propose that the import of extracellular dsRNA into the germline tunes intracellular pathways that cause heritable RNA silencing." This is important because C. elegans small RNA pathways differ significantly from those in other organisms, particularly in the PIWI-interacting RNA (piRNA) pathways, which depend on dsRNA in C. elegans but uses ssRNA in vertebrates. Specification is crucial to prevent misinterpretation by the reader. It is well understood that mechanisms of transgenerational inheritance that operate in nematodes or plants are not conserved in mammals.

• The first sentence of the discussion, "Our analyses suggest a model for ...", would also benefit from specifying "in C. elegans". The same applies to the figure captions. Clarification of the model organism should be added to the first sentence, especially in Figure 1.

Reviewer #2 (Public review):

Summary:

RNAs can function across cell borders and animal generations as sources of epigenetic information for development and immunity. The specific mechanistic pathways how RNA travels between cells and progeny remains an open question. Here, Shugarts, et al. use molecular genetics, imaging, and genomics methods to dissect specific RNA transport and regulatory pathways in the C. elegans model system. Larvae ingesting double stranded RNA is noted to not cause continuous gene silencing throughout adulthood. Damage of neuronal cells expressing double stranded target RNA is observed to repress target gene expression in the germline. Exogenous supply of short or long double stranded RNA required different genes for entry into progeny. It was observed that the SID-1 double-stranded RNA transporter showed different expression over animal development. Removal of the sid-1 gene caused upregulation of two genes, the newly described sid-1-dependent gene sdg-1 and sdg-2. Both genes were observed to also be negatively regulated by other small RNA regulatory pathways. Strikingly, loss then gain of sid-1 through breeding still caused variability of sdg-1 expression for many, many generations. SDG-2 protein co-localizes with a Z-granule marker, an intracellular site for heritable RNA silencing machinery. Collectively, sdg-1 presents a model to study how extracellular RNAs can buffer gene expression in germ cells and other tissues.

Strengths:

(1) Very clever molecular genetic methods and genomic analyses, paired with thorough genetics, were employed to discover insights into RNA transport, sdg-1 and sdg-2 as sid-1-dependent genes, and sdg-1's molecular phenotype.

(2) The manuscript is well cited, and figures reasonably designed.

(3) The discovery of the sdg genes being responsive to the extracellular RNA cell import machinery provides a model to study how exogenous somatic RNA is used to regulate gene expression in progeny. The discovery of genes within retrotransposons stimulates tantalizing models how regulatory loops may actually permit the genetic survival of harmful elements.

Weaknesses:

(1) As presented, the manuscript is incredibly broad, making it challenging to read and consider the data presented. This concern is exemplified in the model figure, that requires two diagrams to summarize the claims made by the manuscript.

(2) The large scope of the manuscript denies space to further probe some of the ideas proposed. The first part of the manuscript, particularly Figures 1 and 2, presents data that can be caused by multiple mechanisms, some of which the authors describe in the results but do not test further. Thus, portions of the results text come across as claims that are not supported by the data presented.

(3) The manuscript focuses on the genetics of SDGs but not the proteins themselves. Few descriptions of the SDGs functions are provided nor is it clarified why only SDG-1 was pursued in imaging and genetic experiments. Additionally, the SDG-1 imaging experiments could use additional localization controls.

eLife assessment

The fruit fly brain hosts neurosecretory neurons (Insulin Producing Cells or IPCs) that integrate many inputs and release insulin directly into the hemolymph. In this fundamental study, the population of IPCs are shown to be heterogeneous in their receptor diversity, exhibiting a range of responses to neuromodulation. The authors convincingly demonstrate, using a battery of experimental techniques and relying on the mapped whole brain connectome, how the heterogeneity in the responses across individual IPCs occur simultaneously and together modulate insulin release to maintain metabolic homeostasis. This work will be of interest to neuroscientists and physiologists, in particular for how cellular diversity results in a better control of homeostasis in short time scales.

Reviewer #1 (Public review):

Summary:

Insulin is crucial for maintaining metabolic homeostasis, and its release is regulated by various pathways, including blood glucose levels and neuromodulatory systems. The authors investigated the role of neuromodulators in regulating the dynamics of the adult Drosophila IPC population. They showed that IPCs express various receptors for monoaminergic and peptidergic neuromodulators, as well as synaptic neurotransmitters with highly heterogeneous profiles across the IPC population. Activating specific modulatory inputs, e.g. dopaminergic, octopaminergic or peptidergic (Leucokinin) using an optogenetic approach coupled with in vivo electrophysiology unveiled heterogeneous responses of individual IPCs resulting in excitatory, inhibitory or no responses. Interestingly, calcium imaging of the entire IPC population with or without simultaneous electrophysiological recording of individual cells showed highly specific and stable responses of individual IPCs suggesting their intrinsic properties are determined by the expressed receptor repertoire. Using the adult fly connectome they further corroborate the synaptic input of excitatory and inhibitory neuronal subsets of IPCs. The authors conclude that the heterogeneous modulation of individual IPC activity is more likely to allow for flexible control of insulin release to adapt to changes in metabolic demand and environmental cues.

Strengths:

This study provides a comprehensive, multi-level analysis of IPC properties utilizing single-nucleus RNA sequencing, anatomical receptor expression mapping, connectomics, electrophysiological recordings, calcium-imaging and an optogenetics-based 'intrinsic pharmacology' approach. It highlights the heterogeneous receptor profiles of IPCs, demonstrating complex and differential modulation within the IPC population. The authors convincingly showed that different neuromodulatory inputs exhibit varied effects on IPC activity and simultaneous occurrence of heterogeneous responses in IPCs with some populations exciting a subset of IPCs while inhibiting others, showcasing the intricate nature of IPC modulation and diverse roles of IPC subgroups. The temporal dynamic of IPC modulation showed that polysynaptic and neuromodulatory connections play a major role in IPC response. The authors demonstrated that certain neuromodulatory inputs, e.g. dopamine, can shift the overall IPC population activity towards either an excited or inhibited state. The study thus provides a fundamental entry point to understanding the complex influence of neuromodulatory inputs on the insulinergic system of Drosophila.

Weakness:

GPCRs are typically expressed at low levels and while the transcriptomic and reporter expression analysis was comprehensive, both approaches have the caveat that they do not allow validating protein level expression. Thus, some receptors might have been missed while others might be false positives. The authors acknowledged the challenges in accurately accessing receptor expression in complex modulatory systems indicating there are limitations in full understanding of the receptor profiles of IPCs.

While this study provides valuable insights into the heterogeneity of IPC responses and receptor expression, it will require future studies to elucidate how these modulatory inputs affect insulin release and transcriptional long-term changes.<br /> The authors further analyzed male and female snRNAseq data and claimed that the differences in receptor expression were minimal. The experimental analyses used mated females only and while the study is very complete in this respect, it would have been extremely interesting to compare male flies in terms of their response profiles.<br /> Lastly as also pointed out by the authors, their approach of using optogenetically driven excitation of modulatory neuronal subsets limits the interpretation of the results due to the possibly confounding direct or indirect effect of fast synaptic transmission on IPC excitation/inhibition, and the broad expression of some neuromodulatory lines used in this analysis.

Overall, however, the conclusions of this study are well supported by the data provided by the authors. Moreover, their detailed and thorough analysis of IPC modulation will have a significant impact on the field of metabolic regulation to understand the complex regulatory mechanism of insulin release, which can now be studied further to provide insight about metabolic homeostasis and neural control of metabolic processes.

Reviewer #2 (Public review):

Summary:

Held et al. investigated the distinct activities of Insulin-Producing Cells (IPCs) by electrophysiological recordings and calcium imaging. In the brain of the fruit fly Drosophila melanogaster, there are approximately 14 IPCs that are analogous to mammalian pancreatic beta cells and provide a good model system for monitoring their activities in vivo. The authors performed single-nucleus RNA sequencing analysis to examine what types of neuromodulatory inputs are received by IPCs. A variety of neuromodulatory receptors are expressed heterogeneously in IPCs, which would explain the distinct activities of IPCs in response to the activations of neuromodulatory neurons. The authors also conducted the connectome analysis and G-protein prediction analysis to strengthen their hypothesis that the heterogeneity of IPCs may underlie the flexible insulin release in response to various environmental conditions.

Strengths:

The authors succeeded patch-clamp recordings and calcium imaging of individual IPCs in living animals at a single-cell resolution, which allows them to show the heterogeneity of IPCs precisely. They measured IPC activities in response to 9 types of neurons in patch-clamp recordings and 5 types of neurons in calcium imaging, comparing the similarities and differences in activities between two methods. These results support the idea that the neuromodulatory system affects individual IPC activities differently in a receptor-dependent manner.

Weaknesses:

One concern is how much extent the heterogeneity of IPC activities in a short time scale is relevant to the net output, a release of insulin-like peptides in response to metabolic demands in a relatively longer time scale. The authors can test their hypothesis by manipulating the heterogeneous expressions of receptor genes in IPCs and examining IPC activities on a longer time scale. Moreover, while the authors focus on IPC activities, they did not show the activation of the neuromodulatory inputs and the net output of insulin levels in the data. The readers might want to know which neurons are indeed activated to send signals to IPCs and how IPC activities result in the secretion of insulin peptides.

Reviewer #2 (Public Review):

As discussed in the original review, this manuscript is an important contribution to a mechanistic understanding of LRRK2 kinase. Kinetic parameters for the GTPase activity of the ROC domain have been determined in the absence/presence of kinase activity. A feedback mechanism from the kinase domain to GTP/GDP hydrolysis by the ROC domain is convincingly demonstrated through these kinetic analyses. However, a regulatory mechanism directly linking the T1343 phospho-site and a monomer/dimer equilibrium is not fully supported. The T1343A mutant has reduced catalytic activity and can form similar levels of dimer as WT. The revised manuscript does point out that other regulatory mechanisms can also play a role in kinase activity and GTP/GDP hydrolysis (Discussion section). The environmental context in cells cannot be captured from the kinetic assays performed in this manuscript, and the introduction contains some citations regarding these regulatory factors. This is not a criticism, the detailed kinetics here are rigorous, but it is simply a limitation of the approach.

Author Response:

We would like to thank the reviewers for their constructive feedback and for acknowledging that our approach offers a simple yet powerful framework with the potential to serve as a comprehensive and intuitive tool for analyzing functional activity and connectivity.

In response to the reviewers’ recommendations, we will aim to improve and clarify the following aspects of our work in an upcoming revision:

Scope and limitations of the “fcHNN projection” (R#1 and R#2):

Both reviewers have correctly noted that the interpretability and explanatory power of the simplistic, two-dimensional fcHNN-based projection is limited. In the revised manuscript, we will clarify that, indeed, attractors are in a close mathematical relationship with the principal components of the raw data (i.e., the eigenvectors of the connectome) within our framework. The fcHNN-projection was introduced solely to establish a link between the proposed framework and concepts with which the reader may be more familiar.

We will enhance the presentation and discussion of our results to emphasize that – as the reviewers also kindly pointed out - the value of our approach lies in modelling how different facets of brain activity dynamically emerge from a common space of functional (ghost) attractors, rather than studying in the static attractor patterns themselves.

Motivations and Rationale for Using the Functional Connectome (R#2):

We agree with Reviewer #2 that a deeper mechanistic explanatory power could be achieved by modeling structure-function coupling, and that our framework is well-suited for this challenge. In our revision, we will highlight this as one of the promising future applications of our framework. We will, furthermore, clarify that the scope of the present work was deliberately restricted to functional connectivity to demonstrate that our framework also allows us to “bypass” the significant challenge of structure-function coupling. This enables us to focus on understanding the origins of canonical resting-state networks, the dynamic responses of the system to perturbations and the complex relationship between task-induced activity and resting-state connectivity, without first solving the structure-function coupling problem.

Additionally, we will mathematically justify the use of linear measures of the functional connectome to reconstruct the underlying non-linear dynamic system, thereby clearly delineating which results can and cannot be considered circular when starting from the functional connectome.

Improvements in Overall Clarity of Presentation (R#1):

In line with the above points and in general, we will strive to enhance the overall clarity of the presentation of our results, including figures, wording, and statistical analysis.

eLife assessment

This study presents a useful approach for revealing large-scale brain attractor dynamics during resting states, task processing, and disease conditions using insights from Hopfield neural networks. The evidence supporting the findings is solid across the many datasets analysed. The work will be of broad interest to neuroscientists using neuroimaging data with interest in computational modelling of brain activity.

Reviewer #1 (Public Review):

Summary:

Englert et al. proposed a functional connectome-based Hopfield artificial neural network (fcHNN) architecture to reveal attractor states and activity flows across various conditions, including resting state, task-evoked, and pathological conditions. The fcHNN can reconstruct characteristics of resting-state and task-evoked brain activities. Additionally, the fcHNN demonstrates differences in attractor states between individuals with autism and typically developing individuals.

Strengths:

(1) The study used seven datasets, which somewhat ensures robust replication and validation of generalization across various conditions.

(2) The proposed fcHNN improves upon existing activity flow models by mimicking artificial neural networks, thereby enhancing the representational ability of the model. This advancement enables the model to more accurately reconstruct the dynamic characteristics of brain activity.

(3) The fcHNN projection offers an interesting visualization, allowing researchers to observe attractor states and activity flow patterns directly.

Weaknesses:

(1) The fcHNN projection can offer low-dimensional dynamic visualizations, but its interpretability is limited, making it difficult to make strong claims based on these projections. The interpretability should be enhanced in the results and discussion.

(2) The presentation of results is not clear enough, including figures, wording, and statistical analysis, which contributes to the overall difficulty in understanding the manuscript. This lack of clarity in presenting key findings can obscure the insights that the study aims to convey, making it challenging for readers to fully grasp the implications and significance of the research.

Reviewer #2 (Public Review):

Summary:

Englert et al. use a novel modelling approach called functional connectome-based Hopfield Neural Networks (fcHNN) to describe spontaneous and task-evoked brain activity and the alterations in brain disorders. Given its novelty, the authors first validate the model parameters (the temperature and noise) with empirical resting-state function data and against null models. Through the optimisation of the temperature parameter, they first show that the optimal number of attractor states is four before fixing the optimal noise that best reflects the empirical data, through stochastic relaxation. Then, they demonstrate how these fcHNN-generated dynamics predict task-based functional activity relating to pain and self-regulation. To do so, they characterise the different brain states (here as different conditions of the experimental pain paradigm) in terms of the distribution of the data on the fcHNN projections and flow analysis. Lastly, a similar analysis was performed on a population with autism condition. Through Hopfield modeling, this work proposes a comprehensive framework that links various types of functional activity under a unified interpretation with high predictive validity.

Strengths:

The phenomenological nature of the Hopfield model and its validation across multiple datasets presents a comprehensive and intuitive framework for the analysis of functional activity. The results presented in this work further motivate the study of phenomenological models as an adequate mechanistic characterisation of large-scale brain activity.

Following up on Cole et al. 2016, the authors put forward a hypothesis that many of the changes to the brain activity, here, in terms of task-evoked and clinical data, can be inferred from the resting-state brain data alone. This brings together neatly the idea of different facets of brain activity emerging from a common space of functional (ghost) attractors.

The use of the null models motivates the benefit of non-linear dynamics in the context of phenomenological models when assessing the similarity to the real empirical data.

Weaknesses:

While the use of the Hopfield model is neat and very well presented, it still begs the question of why to use the functional connectome (as derived by activity flow analysis from Cole et al. 2016). Deriving the functional connectome on the resting-state data that are then used for the analysis reads as circular. If the fcHNN derives the basins of four attractors that reflect the first two principal components of functional connectivity, it perhaps suffices to use the empirically derived components alone and project the task and clinical data on it without the need for the fcHNN framework.

As presented here, the Hopfield model is excellent in its simplicity and power, and it seems suited to tackle the structure-function relationship with the power of going further to explain task-evoked and clinical data. The work could be strengthened if that was taken into consideration. As such the model would not suffer from circularity problems and it would be possible to claim its mechanistic properties. Furthermore, as mentioned above, in the current setup, the connectivity matrix is based on statistical properties of functional activity amongst regions, and as such it is difficult to talk about a certain mechanism. This contention has for example been addressed in the Cole et al. 2016 paper with the use of a biophysical model linking structure and function, thus strengthening the mechanistic claim of the work.

eLife assessment

This paper provides a useful analysis of the variation of the burden of strokes across geographic regions, finding differences in the relationship between strokes and their comorbidities. This dataset and the correlations found within will be a resource for directing the focus of future investigations. The results are technically solid, but there are cases where statistical analyses are yet to be carried out to support statements of statistical significance.

Reviewer #2 (Public Review):

Summary:

The authors have analyzed ethnogeographic differences in the comorbidity factors, such as a diabetes and heart disease, for the incidences of stroke and whether it leads to mortality.

Strengths:

The idea is interesting and data are compelling. The results are technically solid when presented, but in many cases statistical analyses are yet to be carried out to support statements of statistical significance.

The authors identify specific genetic loci that increase the risk of a stroke and how they differ by region.

Weaknesses:

The presentation is not focused. It is important to include p-values for all comparisons and focus the presentation on the main effects from the dataset analysis.

Reviewer #1 (Public Review):

Kreeger and colleagues have explored the balance of excitation and inhibition in the cochlear nucleus octopus cells of mice using morphological, electrophysiological, and computational methods. On the surface, the conclusion, that synaptic inhibition is present, does not seem like a leap. However, the octopus cells have been in the past portrayed as devoid of inhibition. This view was supported by the seeming lack of glycinergic fibers in the octopus cell area and the lack of apparent IPSPs. Here, Kreeger et al. used beautiful immunohistochemical and mouse genetic methods to quantify the inhibitory and excitatory boutons over the complete surface of individual octopus cells and further analysed the proportions of the different subtypes of spiral ganglion cell inputs. I think the analysis stands as one of the most complete descriptions of any neuron, leaving little doubt about the presence of glycinergic boutons.

Kreeger et al then examined inhibition physiologically, but here I felt that the study was incomplete. Specifically, no attempt was made to assess the actual, biological values of synaptic conductance for AMPAR and GlyR. Thus, we don't really know how potent the GlyR could be in mediating inhibition. Here are some numbered comments:

(1) "EPSPs" were evoked either optogenetically or with electrical stimulation. The resulting depolarizations are interpreted to be EPSPs. However previous studies from Oertel show that octopus cells have tiny spikes, and distinguishing them from EPSPs is tricky. No mention is made here about how or whether that was done. Thus, the analysis of EPSP amplitude is ambiguous.

(2) For this and later analysis, a voltage clamp of synaptic inputs would have been a simple alternative to avoid contaminating spikes or shunts by background or voltage-gated conductances. Yet only the current clamp was employed. I can understand that the authors might feel that the voltage clamp is 'flawed' because of the failure to clamp dendrites. But that may have been a good price to pay in this case. The authors should have at least justified their choice of method and detailed its caveats.

(3) The modeling raised several concerns. First, there is little presentation of assumptions, and of course, a model is entirely about its assumptions. For example, what excitatory conductance amplitudes were used? The same for inhibitory conductance? How were these values arrived at? The authors note that EPSGs and IPSGs had peaks at 0.3 and 3 ms. On what basis were these numbers obtained? The model's conclusions entirely depend on these values, and no measurements were made here that could have provided them. Parenthetical reference is made to Figure S5 where a range of values are tested, but with little explanation or justification.

(4) In experiments that combined E and I stimulation, what exactly were time timecourses of the conductance changes, and how 'synchronous' were they, given the different methods to evoke them? (had the authors done voltage clamp they would know the answers).

(5) Figure 4G is confusing to me. Its point, according to the text, is to show that changes in membrane properties induced by a block of Kv and HCN channels would not be expected to alter the amplitudes of EPSCs and IPSCs across the dendritic expanse. Now we are talking about currents (not shunting effects), and the presumption is that the blockers would alter the resting potential and thus the driving force for the currents. But what was the measured membrane potential change in the blockers? Surely that was documented. To me, the bigger concern (stated in the text) is whether the blockers altered exocytosis, and thus the increase in IPSP amplitude in blockers is due BOTH to loss of shunting and increase in presynaptic spike width. Added to this is that 4AP will reduce the spike threshold, thus allowing more ChR2-expressing axons to reach the threshold. Figure 4G does not address this point.

(6) Figure 5F is striking as the key piece of biological data that shows that inhibition does reduce the amplitude of "EPSPs" in octopus cells. Given the other uncertainties mentioned, I wondered if it makes sense as an example of shunting inhibition. Specifically, what are the relative synaptic conductances, and would you predict a 25% reduction given the actual (not modeled) values?

(7) Some of the supplemental figures, like 4 and 5, are hardly mentioned. Few will glean anything from them unless the authors direct attention to them and explain them better. In general, the readers would benefit from more complete explanations of what was done.

Reviewer #2 (Public Review):

Summary:

Kreeger et.al provided mechanistic evidence for flexible coincidence detection of auditory nerve synaptic inputs by octopus cells in the mouse cochlear nucleus. The octopus cells are specialized neurons that can fire repetitively at very high rates (> 800 Hz in vivo), yield responses dominated by the onset of sound for simple stimuli, and integrate auditory nerve inputs over a wide frequency span. Previously, it was thought that octopus cells received little inhibitory input, and their integration of auditory input depended principally on temporally precise coincidence detection of excitatory auditory nerve inputs, coupled with a low input resistance established by high levels of expression of certain potassium channels and hyperpolarization-activated channels.

In this study, the authors used a combination of numerous genetic mouse models to characterize synaptic inputs and enable optogenetic stimulation of subsets of afferents, fluorescent microscopy, detailed reconstructions of the location of inhibitory synapses on the soma and dendrites of octopus cells, and computational modeling, to explore the importance of inhibitory inputs to the cells. They determined through assessment of excitatory and inhibitory synaptic densities that spiral ganglion neuron synapses are densest on the soma and proximal dendrite, while glycenergic inhibitory synaptic density is greater on the dendrites compared to the soma of octopus cells. Using different genetic lines, the authors further elucidated that the majority of excitatory synapses on the octopus cells are from type 1a spiral ganglion neurons, which have low response thresholds and high rates of spontaneous activity. In the second half of the paper, the authors employed electrophysiology to uncover the physiological response of octopus cells to excitatory and inhibitory inputs. Using a combination of pharmacological blockers in vitro cellular and computational modeling, the authors conclude that glycine in fact evokes IPSPs in octopus cells; these IPSPs are largely shunted by the high membrane conductance of the cells under normal conditions and thus were not clearly evident in prior studies. Pharmacological experiments point towards a specific glycine receptor subunit composition. Lastly, Kreeger et. al demonstrated with in vitro recordings and computational modeling that octopus cell inhibition modulates the amplitude and timing of dendritic spiral ganglion inputs to octopus cells, allowing for flexible coincidence detection.

Strengths:

The work combines a number of approaches and complementary observations to characterize the spatial patterns of excitatory and inhibitory synaptic input, and the type of auditory nerve input to the octopus cells. The combination of multiple mouse lines enables a better understanding of and helps to define, the pattern of synaptic convergence onto these cells. The electrophysiology provides excellent functional evidence for the presence of the inhibitory inputs, and the modeling helps to interpret the likely functional role of inhibition. The work is technically well done and adds an interesting dimension related to the processing of sound by these neurons. The paper is overall well written, the experimental tests are well-motivated and easy to follow. The discussion is reasonable and touches on both the potential implications of the work as well as some caveats.

Weaknesses:

While the conclusions presented by the authors are solid, a prominent question remains regarding the source of the glycinergic input onto octopus cells. In the discussion, the authors claim that there is no evidence for D-stellate, L-stellate, and tuberculoventral cell (all local inhibitory neurons of the ventral and dorsal cochlear nucleus) connections to octopus cells, and cite the relevant literature. An experimental approach will be necessary to properly rule out (or rule in) these cell types and others that may arise from other auditory brainstem nuclei. Understanding which cells provide the inhibitory input will be an essential step in clarifying its roles in the processing of sound by octopus cells.

The authors showed that type 1a SGNs are the most abundant inputs to octopus cells via microscopy. However, in Figure 3 they compare optical stimulation of all classes of ANFs, then compare this against stimulation of type 1b/c ANFs. While a difference in the paired-pulse ratio (and therefore, likely release probability) can be inferred by the difference between Foxg1-ChR2 and Ntng1-ChR2, it would have been preferable to have specific data with selective stimulation of type 1a neurons.

eLife assessment

This valuable study, which implicates a specific Wolbachia gene in driving the male-killing phenotype in a moth, contributes to a growing body of literature from the authors in which they have nicely teased apart the loci responsible for male killing across diverse insects. Solid evidence supports the conclusions, though improvements to the statistical analysis for certain assays would strengthen the inferences further.

Reviewer #1 (Public review):

Summary:

Insects and their relatives are commonly infected with microbes that are transmitted from mothers to their offspring. A number of these microbes have independently evolved the ability to kill the sons of infected females very early in their development; this male killing strategy has evolved because males are transmission dead-ends for the microbe. A major question in the field has been to identify the genes that cause male killing and to understand how they work. This has been especially challenging because most male-killing microbes cannot be genetically manipulated. This study focuses on a male-killing bacterium called Wolbachia. Different Wolbachia strains kill male embryos in beetles, flies, moths, and other arthropods. This is remarkable because how sex is determined differs widely in these hosts. Two Wolbachia genes have been previously implicated in male-killing by Wolbachia: oscar (in moth male-killing) and wmk (in fly male-killing). The genomes of some male-killing Wolbachia contain both of these genes, so it is a challenge to disentangle the two.

This paper provides strong evidence that oscar is responsible for male-killing in moths. Here, the authors study a strain of Wolbachia that kills males in a pest of tea, Homona magnanima. Overexpressing oscar, but not wmk, kills male moth embryos. This is because oscar interferes with masculinizer, the master gene that controls sex determination in moths and butterflies. Interfering with the masculinizer gene in this way leads the (male) embryo down a path of female development, which causes problems in regulating the expression of genes that are found on the sex chromosomes.

Strengths:

The authors use a broad number of approaches to implicate oscar, and to dissect its mechanism of male lethality. These approaches include:<br /> (1) Overexpressing oscar (and wmk) by injecting RNA into moth eggs.<br /> (2) Determining the sex of embryos by staining female sex chromosomes.<br /> (3) Determining the consequences of oscar expression by assaying sex-specific splice variants of doublesex, a key sex determination gene, and by quantifying gene expression and dosage of sex chromosomes, using RNASeq.<br /> (4) Expressing oscar along with masculinizer from various moth and butterfly species, in a silkmoth cell line.

This extends recently published studies implicating oscar in male-killing by Wolbachia in Ostrinia corn borer moths, although the Homona and Ostrinia oscar proteins are quite divergent. Combined with other studies, there is now broad support for oscar as the male-killing gene in moths and butterflies (i.e. order Lepidoptera). So an outstanding question is to understand the role of wmk. Is it the master male-killing gene in insects other than Lepidoptera and if so, how does it operate?

Weaknesses:

I found the transfection assays of oscar and masculinizer in the silkworm cell line (Figure 4) to be difficult to follow. There are also places in the text where more explanation would be helpful for non-experts (see recommendations).

Reviewer #2 (Public review):

Summary:

Wolbachia are maternally transmitted bacteria that can manipulate host reproduction in various ways. Some Wolbachia induce male killing (MK), where the sons of infected mothers are killed during development. Several MK-associated genes have been identified in Homona magnanima, including Hm-oscar and wmk-1-4, but the mechanistic links between these Wolbachia genes and MK in the native host are still unclear.

In this manuscript, Arai et al. show that Hm-oscar is the gene responsible for Wolbachia-induced MK in Homona magnanima. They provide evidence that Hm-Oscar functions through interactions with the sex determination system. They also found that Hm-Oscar disrupts sex determination in male embryos by inducing female-type dsx splicing and impairing dosage compensation. Additionally, Hm-Oscar suppresses the function of Masc. The manuscript is well-written and presents intriguing findings. The results support their conclusions regarding the diversity and commonality of MK mechanisms, contributing to our understanding of the mechanisms and evolutionary aspects of Wolbachia-induced MK.

Strengths/weaknesses:

(1) The authors found that transient overexpression of Hm-oscar, but not wmk-1-4, in Wolbachia-free H. magnanima embryos induces female-biased sex ratios. These results are striking and mirror the phenotype of the wHm-t infected line (WT12). However, Table 1 lists the "male ratio," while the text presents the "female ratio" with standard deviation. For consistency, the calculation term should be uniform, and the "ratio" should be listed for each replicate.

(2) The error bars in Figure 3 are quite large, and the figure lacks statistical significance labels. The authors should perform statistical analysis to demonstrate that Hm-oscar-overexpressed male embryos have higher levels of Z-linked gene expression.

(3) The authors demonstrated that Hm-Oscar suppresses the masculinizing functions of lepidopteran Masc in BmN-4 cells derived from the female ovaries of Bombyx mori. They should clarify why this cell line was chosen and its biological relevance. Additionally, they should explain the rationale for evaluating the expression levels of the male-specific BmIMP variant and whether it is equivalent to dsx.

(4) Although the authors show that Hm-oscar is involved in Wolbachia-induced MK in Homona magnanima and interacts with the sex determination system in lepidopteran insects, the precise molecular mechanism of Hm-oscar-induced MK remains unclear. Further studies are needed to elucidate how Hm-oscar regulates Homona magnanima genes to induce MK, though this may be beyond the scope of the current manuscript.

Reviewer #3 (Public review):

Summary:

Overall, this is a clearly written manuscript with nice hypothesis testing in a non-model organism that addresses the mechanism of Wolbachia-mediated male killing. The authors aim to determine how five previously identified male-killing genes (encoded in the prophage region of the wHm Wolbachia strain) impact the native host, Homona magnanima moths. This work builds on the authors' previous studies in which:<br /> (1) They tested the impact of these same wHm genes via heterologous expression in Drosophila melanogaster.<br /> (2) They examined the activity of other male-killing genes (e.g., from the wFur Wolbachia strain in its native host: Ostrinia furnacalis moths).

Advances here include identifying which wHm gene most strongly recapitulates the male-killing phenotype in the native host (rather than in Drosophila), and the finding that the Hm-Oscar protein has the potential for male-killing in a diverse set of lepidopterans, as inferred by the cell-culture assays.

Strengths:

Strengths of the manuscript include the reverse genetics approaches to dissect the impact of specific male-killing loci, and the use of a "masculinization" assay in Lepidopteran cell lines to determine the impact of interactions between specific masc and oscar homologs.

Weaknesses:

My major comments are related to the lack of statistics for several experiments (and the data normalization process), and opportunities to make the manuscript more broadly accessible.

The manuscript I think would be much improved by providing more details regarding some of the genes and cross-lineage comparisons. I know some of this is reported in previous publications, but some summary and/or additional analysis would make this current manuscript much more approachable for a broader audience, and help guide readers to specific important findings. For example, a graphic and/or more detail on how the wmk/oscar homologs (within and across Wolbachia strains) differ (e.g., domains, percent divergence, etc) would be helpful for contextualizing some of the results. I recognize the authors discuss this in parts (e.g., lines 223-227), but it does require some bouncing between sections to follow. Similarly, the experiments presented in Figure 4 indicate that Hm-oscar has broad spectrum activity: how similar are the masc proteins from these various lepidopterans? Are they highly conserved? Rapidly evolving? Do the patterns of masc protein evolution provide any hints at how Oscar might be interacting with masc?

It is clear from Figure 1 that the combinations of wmk homologs do not cause male killing on their own. Did the authors test if any of the wmk homologs impact the MK phenotype of oscar? It looks like a previous study tested this in wFur (noted in lines 250-252), but given that the authors also highlight the differences between the wFur-oscar and Hm-oscar proteins, this may be worth testing in this system. Related to this, what is the explanation for why there would be 4 copies of wmk in Hm?

Why are some of the broods male-biased (2/3) rather than ~50:50? (Lines 170-175, Figure 2a). For example, there is a strong male bias in un-hatched oscar-injected and naturally infected embryos, whereas the control uninfected embryos have normal 50:50 sex ratios. It is difficult to interpret the rate of male-killing given that the sex ratios of different sets of zygotes are quite variable.

Figure 2b - it appears there are both male and female bands in the HmOsc male lane. I think this makes sense (likely a partial phenotype due to the nature of the overexpression approach), but this is worth highlighting, especially in the context of trying to understand how much of the MK phenotype might be recapitulated through these methods. Related, there is no negative control for this PCR.

It appears the RNA-seq analysis (Figure 3) is based on a single biological replicate for each condition. And, there are no statistical comparisons that support the conclusions of a shift in dosage compensation. Finally, it is unclear what exactly is new data here: the authors note "The expression data of the wHm-t-infected and non-infected groups were also calculated based on the transcriptome data included in Arai et al. (2023a)" - So, are the data in Figure 3c and 3d a re-print of previous data? The level of dosage compensation inferred by visually comparing the control conditions in 3b and 3d does not appear consistent. With only one biological replicate library per condition, what looks like a re-print of previous data, and no statistical comparisons, this is a weakly supported conclusion.

In Figure 4: There are no statistics to support the conclusions presented here. Additionally, the data have gone through a normalization process, but it is difficult to follow exactly how this was done. The control conditions appear to always be normalized to 100 ("The expression levels of BmImpM in the Masc and Hm-Oscar/Oscar co-transfected cells were normalized by setting each Masc-transfected cell as 100"). I see two problems with this approach:<br /> (1) This has eliminated all of the natural variation in BmImpM expression, which is likely not always identical across cells/replicates.<br /> (2) How then was the percentage of BmImpM calculated for each of the experimental conditions? Was each replicate sample arbitrarily paired with a control sample? This can lead to very different outcomes depending on which samples are paired with each other. The most appropriate way to calculate the change between experimental and control would be to take the difference between every single sample (6 total, 3 control, 3 experimental) and the mean of the control group. The mean of the control can then be set at 100 as the authors like, but this also maintains the variability in the dataset and then eliminates the issue of arbitrary pairings. This approach would also then facilitate statistical comparisons which is currently missing.

Author response:

Reviewer #2 (Public Review):

In this manuscript, Kafri and colleagues assess the contribution of protein degradation to the cell size-dependent accumulation of total protein. This is an interesting line of research that has not previously been explored. Most of the focus on the size-dependence of protein accumulation has been on the synthesis part of the equation. As cells get too big, the efficiency of cell growth (mass accumulation per unit mass) decreases. It is argued that this is not due to the loss of the efficiency in protein synthesis, but rather is due to the increased protein degradation in larger cells. It is an interesting hypothesis, that might well be true, but there are some issues with key aspects of the data and other supporting data are quite indirect. More work needs to be done to support the central claims.

We thank the reviewer for appreciating the work is interesting and previously unexplored.

The major issue is that the data supporting the proportional increase in protein synthesis with cell size need to be strengthened. Protein synthesis is measured by the amount of a methionine analog that is incorporated in a fixed amount of time. Fig. 2 then plots this amount as a function of cell size, which is presumably measured using a total protein dye (this information is not included; incidentally the axis labels should note what the measurement is 'total protein' or 'forward scatter' rather than the more ambiguous 'cell size'). In any case, something is wrong with the cell size measurements in Figure 2 because many cells basically have almost negligible size (near 0) while others have sizes up to 5 or 6 arbitrary units. It makes no sense that there should be a 10-fold or even 100-fold range in cell sizes. For this reason, I can't interpret the data in Figure 2, which is unfortunate since that is a crucial figure for the authors' argument.

The data supporting higher rates of protein degradation per unit mass in large cells suffers from a similar problem as Figure 3E has the same issue as Figure 2 with too many tiny 'cells'.

Yes, the reviewer is correct that we are using a total protein dye (Alexa fluorophore-conjugated succinimidyl ester, abbreviated as SE) to measure cell size. We have included details regarding the methods of cell size (total protein content) measurement in both the Methods (line 463-466) and Results (line 100-102) sections.

Regarding the reviewer’s concern on the cell size range, we apologize for the confusion the figures may have caused. These cell size measurements are within reasonable range and not 10-fold or 100-fold. Please refer to our detailed response above to essential point #1.

Moreover, the reliance on cycloheximide to treat cells and measure reduction in mass isn't ideal since shutting off all protein synthesis is a pretty drastic perturbation. It would have been better to shut off synthesis of a specific protein and measure its degradation in large and small cells while keeping the cells otherwise intact.

We acknowledge that relying on cycloheximide to measure changes in mass has limitations, as acute inhibition in protein synthesis is a significant perturbation. Ideally, we would measure the degradation of specific proteins in large and small cells while keeping the rest of the cellular processes intact. However, this presents considerable technological challenges. While our evidence clearly shows increased protein degradation and compensatory growth slowdown in large cells, we have not yet identified the specific proteins/genes being targeted. Implementing the reviewer's suggestion would require first screening for a suitable protein/gene to serve as a reporter for compensatory degradation. A significant proteomics screen may allow identification of potential targets, but further validation would necessitate substantial effort, including the generation and validation of a reporter system. We agree that this is a valuable experiment to pursue, but it will likely be part of a follow-up study focused on characterizing the specific protein targets and E3 ligases involved in these processes. In the revised manuscript, we discuss these open questions and future directions in line 380-410.

Reviewer #3 (Public Review):

The authors report a previously undocumented role for UPS-mediated protein turnover in size control in human cells. The study builds on previous observations made by the Kafri group that large cells undergo size compensation by reducing their rate of growth. In particular, recent published work by Ginzberg et al showed that CDK2 inhibition is accompanied by long term size compensation in the form of reduced cell growth whereas CDK6 inhibition is not. The authors investigate the basis for this effect and demonstrate in both unperturbed and perturbed growth/division contexts, using both fixed cells and time lapse microscopy, that the rate of protein synthesis increases proportionately in large cells that undergo size compensation even though mass accumulation is attenuated. The authors show that this effect appears to be mediated by increased proteasomal activity, as demonstrated by proteasome-dependent K48-ubiquitin chain turnover. Intriguingly, this degradation-mediated size compensation mechanism appears to be most active at the G1/S transition, the primary point at which size control operates. The experiments are well controlled, and the conclusions of the study are in general well supported by the data. The authors present an interesting set of discussion points that relate their observations to size control mechanisms in dividing and non-dividing cells. While specific mechanisms are not pursued, this study nevertheless adds an important new insight into the still unsolved problem of size control.

We thank the reviewer for appreciating the novelty of the work.

eLife assessment

This important study advances our understanding of the mechanisms underlying chromatin-mediated gene regulation by SET DOMAIN-CONTAINING PROTEIN 7 (SDG7). The evidence supporting the author's claims – centered on a combination of imaging approaches with molecular and genetic experiments – is convincing, although certain aspects can be improved. The work will be of broad interest to molecular biologists studying epigenetic regulation of gene expression.

eLife assessment

The authors conduct a valuable GWAS meta-analysis for COVID-19 hospitalization in admixed American populations and prioritized risk variants and genes. The evidence supporting the claims of the authors is solid. The work will be of interest to scientists studying the genetic basis of COVID pathogenesis.

Reviewer #1 (Public Review):

Summary:

This paper conducted a GWAS meta-analysis for COVID-19 hospitalization among admixed American populations. The authors identified four genome-wide significant associations, including two novel loci (BAZ2B and DDIAS), and an additional risk locus near CREBBP using cross-ancestry meta-analysis. They utilized multiple strategies to prioritize risk variants and target genes. Finally, they constructed and assessed a polygenic risk score model with 49 variants associated with critical COVID-19 conditions.

Strengths:

Given that most of the previous studies were done in European ancestries, this study provides unique findings about the genetics of COVID-19 in admixed American populations. The GWAS data would be a valuable resource for the community. The authors conducted comprehensive analyses using multiple different strategies, including Bayesian fine mapping, colocalization, TWAS, etc., to prioritize risk variants and target genes. The polygenic risk score (PGS) result demonstrated the ability of cross-population PGS model for COVID-19 risk stratification.

Weaknesses:

(1) One of the major limitations of this study is that the GWAS sample size is relatively small, which limits its power.<br /> (2) Lack of replication cohort.<br /> (3) Colocalization and TWAS used eQTL data from GTEx data, which are mainly from European ancestries.

Comments on latest version:

The authors addressed most of my concerns.

Reviewer #2 (Public Review):

This is a genome-wide association study of COVID-19 in individuals of admixed American ancestry (AMR) recruited from Brazil, Colombia, Ecuador, Mexico, Paraguay and Spain. After quality control and admixture analysis, a total of 3,512 individuals were interrogated for 10,671,028 genetic variants (genotyped + imputed). The genetic association results for these cohorts were meta-analyzed with the results from The Host Genetics Initiative (HGI), involving 3,077 cases and 66,686 controls. The authors found two novel genetic loci associated with COVID-19 at 2q24.2 (rs13003835) and 11q14.1 (rs77599934), and other two independent signals at 3p21.31 (rs35731912) and 6p21.1 (rs2477820) already reported as associated with COVID-19 in previous GWASs. Additional meta-analysis with other HGI studies also suggested risk variants near CREBBP, ZBTB7A and CASC20 genes.

Strengths:

These findings rely on state-of-the-art methods in the field of Statistical Genomics and help to address the issue of low number of GWASs in non-European populations, ultimately contributing to reduce health inequalities across the globe.

Weaknesses:

There is no replication cohort, as acknowledged by the authors (page 29, line 587) and no experimental validation to assess the biological effect of putative causal variants/genes. Thus, the study provides good evidence of association, rather than causation, between the genetic variants and COVID-19.

Comments on latest version:

The issues identified in the first round of review were well addressed by the authors in the revised version of the manuscript.

Reviewer #3 (Public Review):

Summary:

In the context of the SCOURGE consortium's research, the authors conduct a GWAS meta-analysis on 4,702 hospitalized individuals of admixed American descent suffering from COVID-19. This study identified four significant genetic associations, including two loci initially discovered in Latin American cohorts. Furthermore, a trans-ethnic meta-analysis highlighted an additional novel risk locus in the CREBBP gene, underscoring the critical role of genetic diversity in understanding the pathogenesis of COVID-19.

Strengths:

(1) The study identified two novel severe COVID-19 loci (BAZ2B and DDIAS) by the largest GWAS meta-analysis for COVID-19 hospitalization in admixed Americans.<br /> (2) With a trans-ethnic meta-analysis, an additional risk locus near CREBBP was identified.

Weaknesses:

(1) The GWAS power is limited due to the relatively small number of cases.

(2) There is no replication study for the novel severe COVID-19 loci, which may lead to false positive findings.

(3) The variants selected for the PGS appear arbitrary and may not leverage the GWAS findings.

(4) The TWAS models were predominantly trained on European samples, and there is no replication study for the findings as well.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper conducted a GWAS meta-analysis for COVID-19 hospitalization among admixed American populations. The authors identified four genome-wide significant associations, including two novel loci (BAZ2B and DDIAS), and an additional risk locus near CREBBP using cross-ancestry meta-analysis. They utilized multiple strategies to prioritize risk variants and target genes. Finally, they constructed and assessed a polygenic risk score model with 49 variants associated with critical COVID-19 conditions.

Strengths:

Given that most of the previous studies were done in European ancestries, this study provides unique findings about the genetics of COVID-19 in admixed American populations. The GWAS data would be a valuable resource for the community. The authors conducted comprehensive analyses using multiple different strategies, including Bayesian fine mapping, colocalization, TWAS, etc., to prioritize risk variants and target genes. The polygenic risk score (PGS) result demonstrated the ability of the cross-population

PGS model for COVID-19 risk stratification.

Thank you very much for the positive comments and the willingness to revise this manuscript.

Weaknesses:

(1) One of the major limitations of this study is that the GWAS sample size is relatively small, which limits its power.

(2) The fine mapping section is unclear and there is a lack of information. The authors assumed one causal signal per locus, and only provided credible sets, but did not provide posterior inclusion probabilities (PIP) for the variants to be causal.

(3) Colocalization and TWAS used eQTL data from GTEx data, which are mainly from European ancestries. It is unclear how much impact the ancestry mismatch would have on the result. The readers should be cautious when interpreting the results and designing follow-up studies.

We agree with that the sample size is relatively small. Despite that, it was sufficient to reveal novel risk loci supporting the robustness of the main findings. We have indicated this limitation at the end of the discussion section.

Thank you for rising this point. As suggested, we have also used SuSIE, which allows to assume more than one causal signal per locus. However, in this case the results were not different from those obtained with the original Bayesian colocalization performed with corrcoverage. Regarding the PIP, at the fine mapping stage we are inclined to put more weight on the functional annotations of the variants in the credible set than on the statistical contributions to the signal. This is the reason why we prefer not to put weight on the PIP of the variants but prioritize variants that were enriched functional annotations.

This is a good point regarding the lack of diversity in GTEx data. We have also used data from AMR populations (GALA II-SAGE models), although it was only available for blood tissue. Regarding the ancestry mismatch between datasets, several studies have attempted to explore the impact. Gay et al. (PMID: 32912333) studied local ancestry effects on eQTLs from the GTEx consortium and concluded that adjustment of eQTLs by local ancestry only yields modest improvement over using global ancestry (as done in GTEx). Moreover, the colocalization results between adjusting by Local Ancestry and Global Ancestry were not significantly different. Besides, Mogil et al. (PMID: 30096133) observed that genes with higher heritability share genetic architecture between populations. Nevertheless, both studies have evidenced decreased power and poorer predictive performances regarding gene expression because of reduced diversity in eQTL analyses. As consequence of the ancestry mismatch, we now warn the readers that this may compromise signal detection (Discussion, lines 531-533). 

Reviewer #2 (Public Review):

This is a genome-wide association study of COVID-19 in individuals of admixed American ancestry (AMR) recruited from Brazil, Colombia, Ecuador, Mexico, Paraguay, and Spain. After quality control and admixture analysis, a total of 3,512 individuals were interrogated for 10,671,028 genetic variants (genotyped + imputed). The genetic association results for these cohorts were meta-analyzed with the results from The Host Genetics Initiative (HGI), involving 3,077 cases and 66,686 controls. The authors found two novel genetic loci associated with COVID-19 at 2q24.2 (rs13003835) and 11q14.1 (rs77599934), and other two independent signals at 3p21.31 (rs35731912) and 6p21.1 (rs2477820) already reported as associated with COVID-19 in previous GWASs. Additional meta-analysis with other HGI studies also suggested risk variants near CREBBP, ZBTB7A, and CASC20 genes.

Strengths:

These findings rely on state-of-the-art methods in the field of Statistical Genomics and help to address the issue of a low number of GWASs in non-European populations, ultimately contributing to reducing health inequalities across the globe.

Thank you very much for the positive comments and the willingness to revise this manuscript.

Weaknesses:

There is no replication cohort, as acknowledged by the authors (page 29, line 587), and no experimental validation to assess the biological effect of putative causal variants/genes. Thus, the study provides good evidence of association, rather than causation, between the genetic variants and COVID-19. Lastly, I consider it crucial to report the results for the SCOURGE Latin American GWAS, in addition to its meta-analysis with HGI results, since HGI data has a different phenotype scheme (Hospitalized COVID vs Population) compared to SCOURGE (Hospitalized COVID vs Non-hospitalized COVID).

We essentially agree with the reviewer in that one of the main limitations of the study is the lack of a replication stage because of the use of all available datasets on a one-stage analysis. To contribute to the interpretation of the findings in the absence of a replication stage, we now assessed the replicability of the novel loci using the Meta-Analysis Model-based Assessment of replicability (MAMBA) approach (PMID: 33785739) and included the posterior probabilities of replication in Table 2. We also explored further the potential replicability of signals in other populations. We agree that the results should be interpreted in terms of associations given the lack of functional validation of main findings, so we have slightly modified the discussion.

As suggested, the SCOURGE Latin American GWAS summary is now accessible by direct request to the Consortium GitHub repository (https://github.com/CIBERER/Scourge-COVID19) (lines 797-799). We have also included the results from the SCOURGE GWAS analysis for the replication of the 40 lead variants in the Supplementary Table 12. Results from the SCOURGE GWAS for the lead variants in the AMR meta-analysis with HGI were already included in the Supplementary Table 2. As note, we have not been able to conduct the meta-analysis with the same hospitalization scheme as in the HGI study since the population-specific results for those analyses were not publicly released. However, sensitivity analyses included within the supplementary material from the COVID-19 Host Genetics Initiative (2021) stated that there were no significant differences in effects (Odds Ratios) between analyses using population controls or just non-hospitalized COVID-19 patients.

Reviewer #3 (Public Review):

Summary:

In the context of the SCOURGE consortium's research, the authors conduct a GWAS meta-analysis on 4,702 hospitalized individuals of admixed American descent suffering from COVID-19. This study identified four significant genetic associations, including two loci initially discovered in Latin American cohorts. Furthermore, a trans-ethnic meta-analysis highlighted an additional novel risk locus in the CREBBP gene, underscoring the critical role of genetic diversity in understanding the pathogenesis of COVID-19.

Strengths:

(1) The study identified two novel severe COVID-19 loci (BAZ2B and DDIAS) by the largest GWAS meta-analysis for COVID-19 hospitalization in admixed Americans.

(2) With a trans-ethnic meta-analysis, an additional risk locus near CREBBP was identified.

Thank you very much for the positive comments and the willingness to revise this manuscript.

Weaknesses:

(1) The GWAS power is limited due to the relatively small number of cases.

(2) There is no replication study for the novel severe COVID-19 loci, which may lead to false positive findings.

We agree with that the sample size is relatively small. Despite that, it was sufficient to reveal novel risk loci supporting the robustness of the main findings. We have indicated this limitation at the end of the discussion section.

Regarding the lack of a replication study, we now assessed the replicability of the novel loci using the Meta-Analysis Model-based Assessment of replicability (MAMBA) approach (PMID: 33785739). We have included the posterior probabilities of replication in Table 2.

(3) Significant differences exist in the ages between cases and controls, which could potentially introduce biased confounders. I'm curious about how the authors treated age as a covariate. For instance, did they use ten-year intervals? This needs clarification for reproducibility.

Thank you for rising this point. Age was included as a continuous variable. This has been now indicated in line 667 (within Material and Methods).

(4)"Those in the top PGS decile exhibited a 5.90-fold (95% CI=3.29-10.60, p=2.79x10-9) greater risk compared to individuals in the lowest decile". I would recommend comparing with the 40-60% PGS decile rather than the lowest decile, as the lowest PGS decile does not represent 'normal controls'.

Thank you. In the revised version, the PGS categories was compared following the recommendation (lines 461-463).

(5) In the field of PGS, it's common to require an independent dataset for training and testing the PGS model. Here, there seems to be an overfitting issue due to using the same subjects for both training and testing the variants.

We are sorry for the misunderstanding. In fact, we have followed the standard to avoid overfitting of the PGS model and have used different training and testing datasets. The training data (GWAS) was the HGI-B2 ALL meta-analysis, in which our AMR GWAS was not included. The PRS model was then tested in the SCOURGE AMR cohort. However, it is true that we did test the combination of the PRS adding the new discovered variants in the SCOURGE cohort. To avoid potential overfitting by adding the new loci, we have excluded from the manuscript the results on which we included the newly discovered variants.

(6) The variants selected for the PGS appear arbitrary and may not leverage the GWAS findings without an independent training dataset.

Again, we are sorry for the misunderstanding. The PGS model was built with 43 variants associated with hospitalization or severity within the HGI v7 results and 7 which were discovered by the GenOMICC consortium in their latest study and were not in the latest HGI release. The variants are included within the Supplementary Table 14, but we have now annotated the discovery GWAS.

(7) The TWAS models were predominantly trained on European samples, and there is no replication study for the findings as well.

This is a good point regarding the lack of diversity in GTEx data. We have also used data from AMR populations (GALA II-SAGE models), although it was only available for blood tissue. Regarding the ancestry mismatch between datasets, several studies have attempted to explore the impact. Gay et al. (PMID: 32912333) studied local ancestry effects on eQTLs from the GTEx consortium and concluded that adjustment of eQTLs by local ancestry only yields modest improvement over using global ancestry (as done in GTEx). Moreover, the colocalization results between adjusting by Local Ancestry and Global Ancestry were not significantly different. Besides, Mogil et al. (PMID: 30096133) observed that genes with higher heritability share genetic architecture between populations. Nevertheless, both studies have evidenced decreased power and poorer predictive performances regarding gene expression because of reduced diversity in eQTL analyses. As consequence of the ancestry mismatch, we now warn the readers that this may compromise signal detection (Discussion, lines 531-533). 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The authors mentioned the fine mapping method did not converge for the locus in chr 11. I would consider trying a different fine-mapping method (such as SuSiE or FINEMAP). It would be helpful to provide posterior inclusion probabilities (PIP) for the variants in fine mapping results and plot the PIP values in the regional association plots.

As suggested, we have also used SuSIE, which allows to assume more than one causal signal per locus. However, in this case the results were not different from those obtained with the original Bayesian colocalization performed with corrcoverage. SuSIE’s fine-mapping for chromosome 11 prioritized a single variant, which is likely due to the rare frequency. Thus, we have maintained the fine-mapping as it was originally indicated in the previous version of the manuscript but have now included the credible set in Supplementary Table 6.

Regarding the PIP, at the fine mapping stage we are inclined to put more weight on the functional annotations of the variants in the credible set than on the statistical contributions to the signal. This is the reason why we prefer not to put weight on the PIP of the variants but prioritize variants that were enriched functional annotations.

(2) Please provide more detailed information about the VEP and V2G analysis and how to interpret those results. My understanding of V2G is that it includes different sources of information (such as molecular QTLs and chromatin interactions from different tissues/cell types, etc.). It is unclear what sources of information and weight settings were used in the V2G model.

Thank you for rising this point. As suggested, we have clarified the basis for VEP and V2G and the interpretation (lines 732-743).

(3) The authors identified multiple genes with different strategies, e.g. FUMA, V2G, COLOC, TWAS, etc. How many genes were found/supported by evidence provided by multiple methods? It could be helpful to have a table summarizing the risk genes found by different strategies, and the evidence supporting the genes. e.g. which genes are found by which methods, and the biological functions of the genes, etc.

Thank you for rising this point. As suggested, we now added a new figure (Figure 5) to summarize the findings with the multiple methods used.

(4) It would be helpful to make the code/scripts available for reproducibility.

As suggested, the SCOURGE Latin American GWAS summary and the analysis scripts (https://github.com/CIBERER/Scourge-COVID19/tree/main/scripts/novel-risk-hosp-AMR-2024) are now accessible in the Consortium GitHub repository (https://github.com/CIBERER/Scourge-COVID19) (lines 806-807).

(5) The fonts in some of the figures (e.g. Figure 2) are hard to read.

Thank you. We have now included the figures as SVG files.

Reviewer #2 (Recommendations For The Authors):

- The abstract lacks a conclusion sentence.

Thank you. As suggested, we have included two additional sentences with broad conclusions from the study. We preferred to avoid relying on conclusions related to known or new biological links of the prioritized genes given the lack of functional validation of main findings.

- Regarding the association analysis (page 27, line 677), I wonder if some of the 10 principal components (PCs) are capturing information about the recruitment areas (countries). It may be relevant to test for multicollinearity among these variables.

Since we acknowledge that some of the categories might be correlated with a certain PC but not all of them do, we have calculated GVIF values for the main variables to assess the categorical variable as a single entity. The scaled GVIF^1(1/2*Df)) value for the categorical variable is 1.52. Thus, if we square this value, we obtain 2.31, which can be then used for applying usual rule-of-thumb for VIF values.

- Still on the topic of association analysis, did the authors adjust the logistic model for comorbidities variables from Table 1? Given these comorbidities also have a genetic component and their distribution differs between non-hospitalized vs hospitalized, I am concerned that comorbidities might be confounding the association between genetic variants and COVID.

We did not adjust by comorbidities since HGI studies were not adjusted either and we aimed to be as aligned as possible with HGI. However, as suggested, we have now tested the association between each of the comorbidities in Table 1 and each of the variants in Table 2, using the comorbidities as dependent variables and adjusting for the main covariables (age, sex, PCs and country of recruitment). None of the variants were significantly associated to the comorbidities (line 333).

- If I understood correctly, the 49 genetic variants used to develop the polygenic risk score model (PRS) were based on the HGI total sample size (data release 7), which is predominantly of European ancestry. I am concerned about the prediction accuracy in the AMR population (PRS transferability issue).

We have explored literature in search of other PRS to compare the associated OR in our cohort with ORs calculated in European populations. Horowitz et al. (2022) reported an OR of 1.38 for the top 10% with respect to hospitalization risk in European individuals using a GRS with 12 variants.

We acknowledge that this might be an issue and is now explained in discussion of the revised version (lines 561-568). However, as this is the first time a PRS for COVID-19 is applied to a relatively large AMR cohort, we believe that this analysis will be of value for further analyses regarding PRS transferability, providing a source for comparison in further studies.    

- On page 23, line 579, the authors acknowledge their "GWAS is underpowered". This sentence requires a sample/power calculation, otherwise, I suggest using "is likely underpowered".

Thanks for the input. We have modified the sentence as suggested.

Reviewer #3 (Recommendations For The Authors):

I wonder if the authors have an approximate date when the GWAS summary statistic will be available. I reviewed some manuscripts in the past, and the authors claimed they would deposit the data soon, but in fact it would not happen until 2 years later.

The summary statistics are already available from the SCOURGE Consortium repository https://github.com/CIBERER/Scourge-COVID19 (lines 806-807).

eLife assessment

This fundamental study provides convincing evidence for pectin modification as a requirement for RALF peptide signalling altering the apoplastic pH, adding further support for a key role of RALF peptides in linking the assembly and dynamics of the extracellular matrix with cellular activity and function. Data that have been added in comparison to a previous version have enhanced the study. The study should be of interest to anyone studying signaling and specifically to plant cell biologists.

Reviewer #1 (Public review):

Summary:

Rößling et al., report in this study that the perception of RALF1 by the FER receptor is mediated by the association of RALF1 with deesterified pectin, contributing to the regulation of the cell wall matrix and plasma membrane dynamics. In addition, they report that this mode of action is independent from the previously reported cell wall sensing mechanism mediated by the FER-LRX complex.

This manuscript reproduces and aligns with the results from a recently published study (Liu et al., Cell) where they also report that RALF1 can interact with deesterified pectin, forming coacervates and promoting the recruitment of LLG-FER at the membrane.

Reviewer #2 (Public review):

Summary:

The study by Rößling et al. addresses the link between the biochemical constitution of the cell wall, in particular the methylesterification state of pectin with signalling induced by the extracellular RALF peptide. The work suggests that only in the presence of demethylesterifies pectin, RALF is able to trigger activation of its receptor FERONIA (FER).<br /> Remarkably, the application of RALF peptides leads to rather dramatic FER-dependent changes in wall integrity and plasma membrane invaginations not observed before. Interestingly, RALF can be out-titrated from the wall by short pectin fragments. In addition, the study provides further evidence for multiple FER-dependent pathways by showing the presence of LRX proteins is not required for the pectin/RALF mediated signalling.

Strengths:

This work provides fundamental insight into a complex emerging pathway, or perhaps several pathways, linking pectin sensing, pectin structure and RALF/FER signalling. The study provides convincing evidence that pectin methylesterase activity is required for RALF sensing, indicating that the physical interaction of RALFs with the cell wall is important for signalling. Beyond that, the study documents very clearly how profoundly RALF signalling can affect cell wall integrity and membrane topology.

Weaknesses:

Not a weakness per se, as it cannot be avoided, but drawing conclusions from genetic material with altered pectin always suffers from the possibility of secondary effects as this cell wall component is under heavy surveillance and able to respond plastically to different cues. However, the authors take that into account and have performed adequate controls to minimize that possibility.

Reviewer #3 (Public review):

In this important work, the authors show compelling evidence that the Rapid Alkalinisation Factor1 (RALF1) peptide acts as an interlink between pectin methyl esterification status and FERONIA receptor-like kinase in mediating extracellular sensing. Moreover, the RALF1-mediated pectin perception is surprisingly independent of LRX-mediated extracellular sensing in roots. The authors also show that the peptide directly binds demethylated pectin and the positively charged amino acids are required for pectin binding as well as for its physiological activity.

Some present findings are surprising; previously, the FERONIA extracellular domain was shown to bind pectin directly, and the mode of operation in the pollen tube involves the LRX8-RALF4 complex, which seems not the case for RALF1 in the present study. Although some aspects remain controversial, this work is a very valuable addition to the ongoing debate about this elusive complex regulation and signaling.

The authors drafted the manuscript well, so I do not have a lot of criticism or suggestions. The experiments are well-designed, executed, and presented, and they solidly support the authors' claims.

Author response:

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

Reviewer #1 (Recommendations for the Authors):

Major 

(a) In the study the authors focus on the RALF1 peptide. But according to expression data and the study from Abarca et al., 2021, RALF1 is not the only peptide expressed in the root and also having an impact in root growth effect. Similarly, looking at the primary sequence from RALF1 it does not differ much chemically from other RALFs such as RALF33, RALF23, RALF22, etc. So, does the cell wall pectin methylation status also have an impact on the effect of other RALFs on root growth or is that specific of RALF1? 

(b) In addition, is the internalization of FER depending only on RALF1 upon the methylation status of cell wall pectins? Or can other RALFs cause a similar effect potentially?

(c) The authors propose that RALF1 associates with deesterifed pectin, through electrostatic interactions. To do that they perform Biolayer interferometry assays using a buffer with pH 7.4. Is that a relevant pH at the cell wall? Is possible that the authors thought that this may not change the charges of R and K residues, however, it will affect the overall charge of the peptide given the fact that it contains quite some N and Q in the exposed surface. The authors may want to consider that.

(d) Moreover, the authors do not use their peptide RALF1KR, suggested as a peptide not binding OGs, as a control in their OG binding assays. That biochemical experiment should also be included to validate their results and conclusions.

We thank reviewer #1 for these comments. In this work, we focused on RALF1 but the majority of AtRALF peptides, when applied exogenously as synthetic peptides, induce RALF1like effects in Arabidopsis (Abarca et al., 2021; PMID: 34608971). Moreover, all RALF peptides display clusters of R and K residues and are negatively charged (Abarca et al., 2021; PMID: 34608971). In comparison to RALF1, we now also use RALF34 because it was suggested to interact also via the Catharanthus roseus receptor-like kinase 1-like (CrRLK1L) THESEUS1 (THE1). Notably, RALF34 also induced the internalization of FER-GFP. Moreover, the interference with PME also disrupted this activity of RALF34. Therefore, we assume that other RALF peptides display the same or similar signalling modalities. Nevertheless, it remains to be addressed if all RALF family members require PME activity. 

We appreciated these comments and incorporated this aspect in the revised version of the manuscript. The pH was chosen for technical reasons associated with the used BLI buffer. As requested, we also included the RALF1-KR peptide in our OG binding assays. Under these conditions, the mutated peptides were not able to interact with the OGs anymore. Accordingly, we conclude that the K and R residues in RALF1 are crucial for its binding to demethylesterified OGs.  

(e) Another important aspect is regarding their design RALF1KR mutant and its effect in planta. The authors report the following: "RALF1-KR peptides are not bioactive, because they did neither affect root growth, nor cell wall integrity, nor did they induce the ligand-induced endocytosis of FER in epidermal root cells (Figure 5D-I). These findings suggest that the positively charged residues in RALF1 are essential for its activity in roots." According to the structure published by Xiao at el. 2019, the R in the alpha helix from RALF peptides (YISYQSLKR... in RALF1 seq) is directly involved in the interaction with LLGs. So, a mutation in that R may impair the interaction of RALF1 with LLG and therefore the complex formation with FER. So, it is well possible that the effect that the authors are seeing on FER signaling and endocytosis, using this peptide variant, may not be due to the impaired capacity of the peptide to bind deesterified pectin but to not be able to be sensed by the membrane complex directly. To verify that the authors should test, either biochemically or by CoIP in planta, that their RALF1KR variant can still be perceived by the LLG-FER complex. 

We agree with reviewer #1 and do not doubt that the positive charges in RALF1 likely interact with several entities. The respective sites were also covered in Liu et al., 2024 (Cell). It would be interesting to understand how the charge-dependent interaction with pectin modulates the RALF binding to the LLG-FER complex, but these experiments are beyond the scope of this manuscript. We confirmed that the negative charges in RALF1 are essential for OG binding as well as for its bioactivity. We however do not rule out that they bear additional structural functions beyond pectin binding. We clarified this aspect in the revised version. It is conceivable that the pectin and receptor complex binding of RALF1 is molecularly and mechanistically related. 

(f) The authors propose in this study that this effect of RALF1-pectin mode of action on FER is independent from LRXs. That is a very interesting observation which also aligns with similar observations from other independent studies (Moussu et al., 2020; Schoenaers et al. Nat Plants, 2024; Franck et al., 2018). However, that seems to be in conflict with the previous mode of action that the authors had described in Dunser et al., 2019. In that last study the authors had described that FER constitutively interacts with LRX proteins in a direct way to sense cell wall changes. In my view the authors do not critically elaborate to explain these two contradicting results, which are key to understand the mode of action they are describing. This relevant aspect should be addressed more in depth by the authors in their discussion.

Thank you for the comment. We do not see that our findings contradict our previous work (from Dünser et al., 2019). There we concluded that LRX and FER directly interact to sense cell wall characteristics. However, the loss of LRX function abolished the cell wall sensing mechanism, but the respective loss-of-function and dominant negative lines were still able to detect RALF peptides. We hence proposed that the LRX/FER function is at least partially independent of the FER function in RALF perception. This is in agreement with our current study where we conclude again that FER shows LRX-dependent but also -independent modes of action. 

Minor

(g) In the introduction (first page), the authors write the following sentence: "RALF peptides are involved in multiple physiological and developmental processes, ranging from organ growth and pollen tube guidance to modulation of immune responses (Stegmann et al., 2017; Abarca et al., 2021)". RALFs are not involved in pollen tube guidance but pollen tube growth.

So, that should be changed in the Introduction sentence. Also, in addition, the authors could cite additional references here to support the sentence such as Mecchia et al., 2017 or Ge et al. , 2017, in addition. 

Thank you for pointing this out and we apologize for our flaw. We corrected the statement in the revised version of the manuscript and added the citations as requested.

(h) The new study of Schoenaers et al. Nat Plants, 2024 should now be included in the revised version.

Thank you. We implemented this reference in the revised manuscript.

Reviewer #2 (Public Review):

The genetic material used by the authors to strengthen the connection of RALF signalling and

PME activity might not be as suitable as an acute inhibition of PME activity.  The PMEI3ox line generated by Peaucelle et al., 2008 is alcohol-inducible. Was expression of the PMEI induced during the experiments? As ethanol inducible systems can be rather leaky, it would not be surprising if PME activity would be reduced even without induction, but maybe this would warrant testing whether PMEI3 is actually overexpressed and/or whether PME activity is decreased. On a similar note, the PMEI5ox plants do not appear to show the typical phenotype described for this line. I personally don't think these lines are necessary to support the study. Short-term interference with PME activity (such as with EGCG) might be more meaningful than life-long PMEI overexpression, in light of the numerous feedback pathways and their associated potential secondary effects. This might also explain why EGCG leads to an increase in pH, as one would expect from decreased PME activity, while PMEI expression (caveats from above apply) apparently does not (Fig 3A-D).

We agree with reviewer #2. The PMEI3ox line from Peaucelle et al., 2008 is ethanolinducible, but we observed a strong phenotype (at seedling and adult stage) without ethanol induction. We performed all experiments (root growth assays and confocal observations) with as well as without induction using ethanol, leading to similar results. We concluded from that, that the line is either leaky or that overexpression of PMEI3 is already induced upon seed sterilisation with ethanol. Accordingly, we did not intend to use the lines as acute inhibition of PME but rather used the lines to genetically confirm our data derived from acute pharmacological inhibition. We do show in Figure 1G that the levels of de-methylesterified pectin is decreased in the PMEI3ox mutant compared to WT seedlings. It is exactly this alteration that we are exploiting to assess the necessity of charged pectin for RALF1 signalling. Since the apoplastic pH in the PMEI3ox line is not altered compared to WT, we can conclude that the observed effect on RALF1 signalling is entirely due to the altered pectin charge.

We would like to note that the PMEI5ox line indeed shows the reported root-bending phenotype when grown on plates. We started to perform RALF application assays in liquid medium, because EGCG does not show activity on MS plates. Moreover, it allows us to perform the assays with low amounts of synthetic peptides. The seedling images in our root growth assay might be hence misleading since the assay was done in liquid MS medium and the seedlings were carefully straightened on MS plates before imaging. This transfer makes it difficult to observe the root-bending or -curling phenotype, which is typical for PMEI5ox. 

At least at first sight, the observation that OGs are able to titrate RALF from pectin binding seems at odds with the idea of cooperative binding with low affinity, leading to high avidity oligomers. Perhaps the can provide a speculative conceptual model of these interactions?

We added a high concentration of OGs in the media and observed a strong repression of RALF1 activity at the root surface. We assume the OGs form oligomers with RALF peptides in the media, preventing them from penetrating the roots.

I could not find a description of the OG treatment/titration experiments, but I think it would be important to understand how these were performed with respect to OG concentration, timing of the application, etc.

Thank you for pointing this out. The description of the OG RALF titration is added in the methods section.

Reviewer #2 (Recommendations for the Authors):

Page 3: „and can bind to extracellular pectin" Liu et al, 2024 should maybe also be cited here. 

Amended.

I am not so sure about the use of "conceptualizing" in the last sentence of the abstract and elsewhere in the manuscript.

I would suggest adding a few sentences that describe and differentiate what this study and other recently published works (e.g. Dünser, Liu, Mossou, Lin) have revealed about the pectin association of RALFs, LRXs, and FER to help the non-expert reader to navigate this increasingly complex area. May also be worth mentioning that the previously described pectin sensing function of FER is physically separated from the RALF binding domain (Gronnier et al., 2022)

Thank you for your constructive comments. We followed your suggestions and further improved the discussion in the revised version of our manuscript.

Reviewer #3 (Recommendations for the Authors): 

(1) The authors claim that pectin is something like an extracellular signaling scaffold. In other fields, signalling scaffold refers to proteins that tether the signalling components and regulate/are involved in the signal transduction. Here, pectin is a cell wall structural component whose molecular status is sensed and perceived rather than a functional signaling component. To me, it is FERONIA to be called a signalling scaffold in this case. However, this is my view, and the authors may present their concept. 

RALF peptides as well as FERONIA bind to de-methylesterified pectin, which is essential for its signalling output. Albeit not being a protein, we propose that pectin functions like a scaffold tethering both signalling components and thereby enabling signalling. FERONIA has been indeed also proposed to function as a scaffold when tethering other signalling components.

(2) I have no problem with authors using the more general term pectin instead of homogalacturonan throughout the text. Still, authors should, at some point in the text, specify that by pectin, they mean homogalacturonan; the authors did not analyze other pectic types on binding. 

We followed your suggestion.

(3) The authors show that RALF1 binds to OGs with a high avidity. Given the fact that OGs released from homogalacturonan upon pathogen infection are Damage-Associated Molecular Patterns (DAMPs), this opens the possibility that this particular activity of RALF1 might actually function in modulation of immune response. I suggest that authors should not exclude this possibility. 

We fully agree to this possibility for FER-dependent signalling.

(4) Are there any indications that a similar mechanism can be extrapolated to other FERONIA homologs, such as THESEUS or HERCULES? Although it is not essential to comment, I think this could enrich the discussion.

This is a highly interesting research question, which we may follow up in our upcoming studies. RALF34, which is considered a ligand for THESEUS, also induced FER internalization, which was also sensitive to PME inhibition. While this requires further investigation, this finding hints at a common mechanism for FER- and THE-dependent RALF peptides.

(5) I suggest using the model scheme currently in the supplement as a main figure to provide an immediate accessible summary of the findings.

Thank you for the suggestion to add the summary scheme in the main figures. We followed your suggestion.

eLife assessment

This valuable study provides new insight into the disassembly of vimentin filaments and the dependence of this mechanism on net charge, albeit with incomplete evidence. In particular, the experimental replicates are limited (in most cases n=1), there is a lack of quantitative analysis to substantiate claims, inconsistency of the proposed mechanisms with previously published work, and lack of biochemical evidence supporting the observations in cells. Addressing these concerns would strengthen the manuscript and help support the proposed hypothesis on vimentin disassembly.

Reviewer #1 (Public review):

Summary:

The authors investigate the mechanism behind the widely observed but poorly understood phenomenon of reversible vimentin disassembly upon hypotonic challenge. Using permeabilized COS-7 cells expressing vimentin-mEos3.2, the authors demonstrate that vimentin disassembly is not due to lower osmotic pressure but rather due to decreased intracellular ionic strength. They propose a model in which vimentin filament stability is predicted by the protein's net charge and support this idea through approaches that involve (i) manipulating buffer ionic strength, (ii) manipulating buffer pH, or (iii) introducing charged amino acids into the linker of the exogenously expressed vimentin-mEos3.2.

Strengths & Weaknesses:

While the discovery is intriguing and presents an interesting concept, significant shortcomings in experimental design and numerous inconsistencies prevent it from reaching the high standards expected. The lack of reproducibility, inadequate controls, and insufficient quantification make the findings feel very preliminary. Additionally, the authors need to address the apparent discrepancies between their current results and their previous work implicating calpains and altered calcium levels in vimentin disassembly upon hypotonic challenge (which has led to much confusion in the field). This discrepancy should be thoroughly addressed in the discussion with the authors citing their prior work and explaining why it was incorrect.

An additional concern is the relevance of the findings to vimentin biology inside cells. The most important insight in this work is the observation that an isotonic buffer balanced with non-electrolytes (glucose or sorbitol) is sufficient to drive vimentin disassembly. The authors show that vimentin disassembly is not due to changes in osmotic pressure but rather due to a change in the concentration of critical dissolved ions, specifically the number of charged states on vimentin. What is missing is when and how this is controlled within cells under physiological conditions - not just when cells are permeabilized with detergents (conditions that cells rarely survive). Without this deeper dive into vimentin states within cells and how it is controlled, the paper seems very narrow in its focus.

Reviewer #2 (Public review):

The reviewed manuscript "Hypersensitivity of the vimentin cytoskeleton to net-charge states and Coulomb repulsion" presents exciting results on the mechanisms governing the assembly and disassembly of the vimentin cytoskeleton. They show, using live-cell imaging, that changes in the intracellular ionic strength induce rapid and dramatic changes to the integrity of the vimentin cytoskeleton. Interestingly, mutants of vimentin with net positive or negative charges display notably different responses to hypotonic stress (and thus changes to the intracellular ionic strength). Even more interesting, the ionic strength-driven mechanism seems to generalize to the several other intermediate filaments explored here. These results are of high interest to the broader cytoskeleton field. A major caveat is that essentially every experiment in the paper is n=1, showing example images of a single cell. The experiments were not repeated, and the results were not quantified. Purported differences between experimental variables/conditions lack statistical significance. Generalization of the ionic strength-based mechanism is hindered by the fact that only one cell type was tested for each cytoskeletal protein. Another caveat is that the fluorescently tagged vimentin used thoroughly in this work is exogenous and overexpressed; it is unclear if the observed effects would also occur at endogenous concentrations of vimentin. As it is currently presented, it is my opinion that all four main figures in this work - although interesting and quite likely correct - should be interpreted as preliminary data by readers.

Reviewer #3 (Public review):

Summary:

This report analyzes the structure of vimentin, GFAP, and keratin intermediate filament networks in cells that have been subjected to hypotonic stress and other treatments that either alter the ionic strength of the cytoplasm or change the charge density of the intermediate filament.

Strengths:

These experiments expand on the work of references 8 and 9, which showed that the vimentin network rapidly dissociates after hypotonic shock. The cellular imaging uses sophisticated super-resolution techniques and produces some striking images.

Weaknesses:

A fundamental weakness of this study lies in the interpretation, and lack of biochemical evidence for the provocative hypothesis raised that the assembly state of intermediate filaments in a cell is governed by coulomb interactions between charged filaments. Several essential experiments need to be done before this striking hypothesis can be plausibly supported.

(1) First the assembly and disassembly of vimentin filaments needs to be done in vitro systems. If the hypothesis is correct then these same effects will happen with purified vimentin intermediate filaments. These proteins are readily purified from bacterial expression systems and there's a wealth of biophysical data on them, so verifying the predictions of this cell-based model can be realistically tested with purified proteins.

(2) Interpretation of these results explicitly avoids a role for post-translational modifications of vimentin, which are well described and related to filament assembly state. For example, reference 9, which is one of the first discoveries that the vimentin network dissociates under osmotic stress explicitly shows that the vimentin network remains intact if either calcium influx or calpain proteolytic activity is prevented. Hypoosmotic stress will still lead to the same dilution, but the filaments remain intact, apparently contradicting the major interpretation of this paper.

(3) The third issue is that the role of polyelectrolyte effects and especially the importance of divalent cations is scarcely mentioned in the interpretation. There are many studies of how strongly vimentin intermediate filaments interact with divalent cations, in a manner that is relatively insensitive to ionic strength, and these effects need to be taken into account to interpret the cellular data or the hypothesis that coulomb repulsion is the major driver for vimentin disassembly.

eLife assessment

The fundamental study by Ding and colleagues identifies subpopulations of neurons recorded in the monkey subthalamic nucleus (STN) with distinct activity profiles and causal contributions during perceptual decision-making. The combination of neuronal recording, microstimulation, and computational methods provides convincing evidence for a heterogenous neural population that could support multifaceted roles in decision formation. This study should be of wide interest to computational and experimental neuroscientists interested in cognitive function.

Reviewer #2 (Public review):

This study uses single-unit recordings in the monkey STN to examine the evidence for three theoretical models that propose distinct roles for the STN in perceptual decision-making. Importantly, the proposed functional roles are predictive of unique patterns of neural activity. Using k-means clustering with seeds informed by each model's predictions, the current study identified three neural clusters with activity dynamics that resembled those predicted by the described theoretical models. The authors are thorough and transparent in reporting the analyses used to validate the clustering procedure and the stability of the clustering results. To further establish a causal role for the STN in decision-making, the researchers applied microsimulation to the STN and found effects on response times, choice preferences, and latent decision parameters estimated with a drift-diffusion model. Overall, the study provides strong evidence for a functionally diverse population of STN neurons that could indeed support multiple roles involved in perceptual decision-making. The manuscript would benefit from stronger evidence linking each neural cluster to specific decision roles in order to strengthen the overall conclusions.

The interpretation of the results, and specifically, the degree to which the identified clusters support each model, is largely dependent on whether the artificial vectors used as model-based clustering seeds adequately capture the expected behavior under each theoretical model. The manuscript would benefit from providing further justification for the specific model predictions summarized in Figure 1B. Further, although each cluster's activity can be described in the context of the discussed models, these same neural dynamics could also reflect other processes not specific to the models. That is, while a model attributing the STN's role to assessing evidence accumulation may predict a ramping up of neural activity, activity ramping is not a selective correlate of evidence accumulation and could be indicative of a number of processes, e.g., uncertainty, the passage of time, etc.. This lack of specificity makes it challenging to infer the functional relevance of cluster activity and should be acknowledged in the discussion.

Additionally, although the effects of STN microstimulation on behavior provide important causal evidence linking the STN to decision processes, the stimulation results are highly variable and difficult to interpret. The authors provide a reasonable explanation for the variability, showing that neurons from unique clusters are anatomically intermingled such that stimulation likely affects neurons across several clusters. It is worth noting, however, that a substantial body of literature suggests that neural populations in the STN are topographically organized in a manner that is crucial for its role in action selection, providing "channels" that guide action execution. The authors should comment on how the current results, indicative of little anatomical clustering amongst the functional clusters, relates to other reports showing topographical organization.

Overall, the association between the identified clusters and the function ascribed to the STN by each of the models is largely descriptive and should be interpreted accordingly. For example, Figure 3 is referenced when describing which cluster activity is choice/coherence dependent, yet it is unclear what specific criteria and measures are being used to determine whether activity is choice/coherence "dependent." Visually, coherence activity seems to largely overlap in panel B (top row). Is there a statistically significant distinction between low and high coherence in this plot? The interpretation of these plots and the methods used to determine choice/coherence "dependence" needs further explanation.

In general, the association between cluster activity and each model could be more directly tested. At least two of the models assume coordination with other brain regions. Does the current dataset include recordings from any of these regions (e.g., mPFC or GPe) that could be used to bolster claims about the functional relevance of specific subpopulations? For example, one would expect coordinated activity between neural activity in mPFC and Cluster 2 according to the Ratcliff and Frank model. Additionally, the reported drift-diffusion model (DDM) results are difficult to interpret as microsimulation appears to have broad and varied effects across almost all the DDM model parameters. The DDM framework could, however, be used to more specifically test the relationships between each neural cluster and specific decision functions described in each model. Several studies have successfully shown that neural activity tracks specific latent decision parameters estimated by the DDM by including neural activity as a predictor in the model. Using this approach, the current study could examine whether each cluster's activity is predictive of specific decision parameters (e.g., evidence accumulation, decision thresholds, etc.). For example, according to the Ratcliff and Frank model, activity in cluster 2 might track decisions thresholds.

Review of revision

The authors have sufficiently addressed the concerns raised in the initial reviews and have revised their manuscript accordingly. We commend the authors for these efforts and feel that the revisions have strengthened the major claims of the manuscript.

Reviewer #3 (Public review):

Summary:

The authors provide compelling evidence for the causal role of the subthalamic nucleus (STN) in perceptual decision-making. By recording from a large number of STN neurons and using microstimulation, they demonstrate the STN's involvement in setting decision bounds, scaling evidence accumulation, and modulating non-decision time.

Strengths:

The study tested three hypotheses about the STN's function and identified distinct STN subpopulations whose activity patterns support predictions from previous computational models. The experiments are well-designed, the analyses are rigorous, and the results significantly advance our understanding of the STN's multi-faceted role in decision formation.

Weaknesses:

While the study provides valuable insights into the STN's role in decision-making, there are a few areas that could be improved. First, the interpretation of the neural subpopulations' activity patterns in relation to the computational models should be clarified, as the observed patterns may not directly correspond to the specific signals predicted by the models. Second, a neural population model could be employed to better understand how the STN population jointly contributes to decision-making dynamics.

Author response:

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

Review #1:

(1) It would be helpful to explain the criteria for choosing a given number of clusters and for accepting the final clustering solution more clearly. The quantitative results (silhouette plots, Rand index) in Supplementary Figure 2 should perhaps be included in the main figure to justify the parameter choices and acceptance of specific clustering solutions.

We revised the text and added labels to the original Supplementary Figure 2 (now main Figure 4) to clarify how we arrived at the best settings for random-seed clustering. 

(2) It would be helpful to show how the activity profiles in Figure 3 would look like for 3 or 5 (or 6) clusters, to give the reader an impression of how activity profiles recovered using different numbers of clusters would differ.

We added a new figure (Supplementary Figure 4) that shows 5- and 6-cluster results. Note that the same three subpopulations in Figure 3 were reliably identified as distinct clusters even with alternative settings, corroborating the results in the tSNE space (Supplementary Figure 3). 

(3) The authors attempt to link the microstimulation effects to the presence of functional neuron clusters at the stimulation site. How can you rule out that there were other, session-specific factors (e.g., related to the animal's motivation) that affected both neuronal activity and behavior? For example, could you incorporate aspects of the monkey's baseline performance (mean reaction time, fixation breaks, error trials) into the analysis?

We tested the potential influences of monkeys’ motivational states on our observations using two sets of analysis. First, we examined whether motivational state modulated the likelihood of observing a specific type of neural activity in STN. We focused on three measurements of motivational states: the rate of fixation break, the overall error rate, and mean RT. We found that none of these measurements differed significantly among sessions when we encountered different subpopulations (new Supplemental Figure 7), suggesting that motivational state alone cannot explain the differences in activity patterns of the four subpopulations. 

Second, we examined how motivational state may be reflected in the microstimulation results. To clarify, because we interleaved trials with and without microstimulation, the microstimulation effects cannot be solely explained by session-specific factors. However, it is possible that motivational state can modulate the magnitude of microstimulation effects. We performed correlation analysis between microstimulation effects (difference in each fitted DDM parameter between trials with and without microstimulation) and motivational state (fixation break, error rate, mean RT on trials without microstimulation). We did not find significant correlation for any combination (Supplemental Table 1). These results suggest that the motivational state of the monkey had little influence on our recording and microstimulation results. However, because our monkeys operated within a narrow range of strong engagement on the task, we cannot rule out the possibility that STN activity or microstimulation effects could change significantly if the monkeys were not as engaged. We have added these results in a new section titled “Heterogeneous activity patterns and microstimulation effects cannot be explained by variations in motivational state”. 

(4) Line 84: What was the rationale for not including both coherence and reaction time in one multiple regression model?

On the task we used, RT depends strongly on coherence in a nonlinear fashion (e.g., example behavior in now Figure 5). We thus performed regressions using coherence and RT separately. We revised the text in Methods to clarify our rationale (lines 470-473):

“To quantitatively measure each neuron’s task-related modulation, we performed two multiple linear regressions for each running window, separately for coherence and RT because monkeys’ RT strongly depends on coherence on our task:”

Review #2:

The interpretation of the results, and specifically, the degree to which the identified clusters support each model, is largely dependent on whether the artificial vectors used as model-based clustering seeds adequately capture the expected behavior under each theoretical model. The manuscript would benefit from providing further justification for the specific model predictions summarized in Figure 1B.

We added information on the original figure/equations that were the basis of the artificial vectors we constructed for clustering analysis and their abbreviated summary in Figure 1B (first paragraph in section “STN subpopulations can support previously theorized functions”). These vectors were meant to capture prominent features of the predicted activity patterns, in the forms of choice, time, and motion strength dependencies. We also emphasize that we obtained very similar results using random clustering seeds.

Further, although each cluster's activity can be described in the context of the discussed models, these same neural dynamics could also reflect other processes not specific to the models. That is, while a model attributing the STN's role to assessing evidence accumulation may predict a ramping up of neural activity, activity ramping is not a selective correlate of evidence accumulation and could be indicative of a number of processes, e.g., uncertainty, the passage of time, etc. This lack of specificity makes it challenging to infer the functional relevance of cluster activity and should be acknowledged in the discussion.

We thank the reviewer for pointing out the alternative interpretation of these modulation patterns. We have added this caveat in the Discussion (lines 398-401): “It is also possible that the ramping activity reflects alternative roles for the STN in the evaluation of the decision process, the tracking of elapsed time, or both. How these possible roles relate to those of caudate neurons awaits further investigation (Fan et al., 2024)”. 

Additionally, although the effects of STN microstimulation on behavior provide important causal evidence linking the STN to decision processes, the stimulation results are highly variable and difficult to interpret. The authors provide a reasonable explanation for the variability, showing that neurons from unique clusters are anatomically intermingled such that stimulation likely affects neurons across several clusters. It is worth noting, however, that a substantial body of literature suggests that neural populations in the STN are topographically organized in a manner that is crucial for its role in action selection, providing "channels" that guide action execution. The authors should comment on how the current results, indicative of little anatomical clustering amongst the functional clusters, relate to other reports showing topographical organization.

We thank the reviewer for raising this important point. We have added the following text in the Discussion:

“The intermingled subpopulations may appear at odds with the conventional idea of topography in how the STN is organized. For example, the “tripartite model” suggests that STN is segregated by motor, associative, and limbic functions (Parent and Hazrati, 1995); afferents from motor cortices and neurons related to different types of movements are largely somatotopically organized in the STN (DeLong et al., 1985; Nambu et al., 1996); and certain molecular markers are expressed in an orderly pattern in the STN (reviewed in Prasad and Wallén-Mackenzie, 2024). Because we focused on STN neurons that were responsive on a single oculomotor decision task, our sampling was likely biased toward STN subdivisions related to associative function and oculomotor movements. As such, our results do not preclude the presence of topography at a larger scale. Rather, our results underscore the importance of activity patternbased analysis, in addition to anatomy-based analysis, for understanding the functional organization of the STN.”

Figure 3 is referenced when describing which cluster activity is choice/coherence dependent, yet it is unclear what specific criteria and measures are being used to determine whether activity is choice/coherence "dependent." Visually, coherence activity seems to largely overlap in panel B (top row). Is there a statistically significant distinction between low and high coherence in this plot? The interpretation of these plots and the methods used to determine choice/coherence "dependence" needs further explanation.

We added a new figure (Sup Figure 3) that shows the summary of choice and coherence modulation, based on multiple linear regression analysis, for each subpopulation separately. We also updated the description of these activity patterns in Results (lines 122-130):

In general, the association between cluster activity and each model could be more directly tested. At least two of the models assume coordination with other brain regions. Does the current dataset include recordings from any of these regions (e.g., mPFC or GPe) that could be used to bolster claims about the functional relevance of specific subpopulations? For example, one would expect coordinated activity between neural activity in mPFC and Cluster 2 according to the Ratcliff and Frank model.

We agree completely that simultaneous recordings of STN and its afferent/efferent regions (such as mPFC, GPe, SNr, and GPi) would provide valuable insights into the specific roles of STN and the basal ganglia as a whole. Such recordings are outside the scope of the current study but are in our future plans. 

Additionally, the reported drift-diffusion model (DDM) results are difficult to interpret as microstimulation appears to have broad and varied effects across almost all the DDM model parameters. The DDM framework could, however, be used to more specifically test the relationships between each neural cluster and specific decision functions described in each model. Several studies have successfully shown that neural activity tracks specific latent decision parameters estimated by the DDM by including neural activity as a predictor in the model. Using this approach, the current study could examine whether each cluster's activity is predictive of specific decision parameters (e.g., evidence accumulation, decision thresholds, etc.). For example, according to the Ratcliff and Frank model, activity in cluster 2 might track decision thresholds.

We thank the reviewer for the suggested analysis. Because including the neural activity in the model substantially increases model fitting time, we performed a preliminary round of model fitting for 15 neurons (5 neurons closest to each of the cluster centroids). For each neuron, we measured the average firing rates in three windows: 1) a 350 ms window starting from dots onset (“Dots”), 2) a 350 ms window ending at saccade onset (“Presac”), and 3) a variable window starting from dots onset and ending at 100 ms before saccade onset (“Fullview”). For each window, the firing rates were z-scored across trials.  We incorporated the firing rates into two model types. In the “DV” type, the firing rates were assumed to influence three DDM parameters related to evidence accumulation: k, me, and z. In the “Bound” type, the firing rates were assumed to influence three DDM parameters related to decision bound: a, B_alpha, and B_d. In total, we fitted six combinations of firing rates and model types to each neuron. For comparison, we also fitted the standard model without incorporating firing rates. 

As shown in Author response image 1, firing rates of single STN neurons had minimal contributions to the fits. With the exception of one neuron, AIC values were greater for model variants including firing rates than the standard model (Author response image 1A), indicating that including firing rate did not improve the fits. For all neurons, the actual fitted coefficients for firing rates were several degrees of magnitude smaller than the corresponding DDM parameter (Author response image 1B; note the range of y axis), indicating that the trial-by-trial variation in firing rate had little influence on the evidence accumulation- or decision bound-related parameters. Based on these preliminary fitting results, we believe that a single STN neuron does not have strong enough influence on the overall evidence accumulation or decision bound to be detected with the model fitting method.  We therefore did not expand the fitting analysis to all neurons. 

Author response image 1.

Firing rates of a single STN neuron did not substantially influence decision-related DDM parameters. A, Differences in AIC between DDM variants that included firing rate-dependent terms and the standard DDM. Red dahsed line: difference = -3. Each column represents results from one unit. B, Fitted coefficients for firing rate-related terms were near zero. Note the range of y axis. Values for the top and bottomw panels were obtained from "DV"- and "Bound"-type models, respectively. See text for more details.

We emphasize, however, that the apparent negative results do not necessarily argue against a causal role of the STN in decision making, rather, these results more likely reflect the methodological limitation: because we used a single task context, the monkeys’ natural trial-by- trial variations in the DDM components may be too small. A better design would be to manipulate task contexts to induce larger changes in evidence accumulation or decision bounds and then test for a correlation between single-neuron firing rates and these changes. We are currently using such a design in a follow-up study. 

The table in Figure 1B nicely outlines the specific neural predictions for each theoretical model but it would help guide the reader if the heading for each column also included a few summary words to remind the reader of the crux of each theory, e.g. "Ratcliff+Frank 2012 (adjusted decision-bounds)"

We thank the reviewer for this suggestion. We considered implementing this but eventually decided not to add more headings to the column, because the predicted STN functions of the three models cannot all be succinctly summarized. We thus prefer to include more detailed descriptions in the main text, instead of in the figure. 

The authors frequently refer to contralateral vs. ipsilateral decisions but never explicitly state what this refers to, i.e. contralateral relative to what (visual field, target direction, recording site, etc.)? The reader can eventually deduce that this means contralateral to the recording site but this should be explicitly stated for clarity.

We added in Methods: 

Line 483: “Contralateral/ipsilateral choices refer to saccades toward the targets contralateral/ipsilateral to the recording sites, respectively.” 

Line 535: Contralateral/ipsilateral choices refer to saccades toward the targets contralateral/ipsilateral to the microstimulation sites, respectively.”

Again, for clarity, it would be helpful to explicitly define what the authors mean by "sensitive to choice" when referring to Figure 1B as this could be interpreted to mean left/right or ipsilateral/contralateral.

In the context of Figure 1B, “sensitive to choice” means showing different responses for the two choices in our 2AFC task, regardless of the task geometry. We added explanation in the figure caption.

Color bar labels would be helpful to include in all figures that include plots with color bars.

We apologize for omitting the labels. They are added to Figure 2B and C, Supplemental Fig. 1.  

The authors should briefly note what a "lapse term" is when describing the logistic function results.

We revised the text in Results (lines 184-186) and Methods (line 527) to clarify that lapse terms were used to capture errors independent of motion strength.

Are the 3 example sessions in Figure 4 stimulating the same STN site and/or the same monkey? This information should be noted in the caption or main text.

We revised the caption: “A-C, Monkey’s choice (top) and RT (bottom) performance for trials with (red) and without (black) microstimulation for three example sessions (A,B: two sites in monkey C; C: monkey F).”

Figure 3B the authors note that "the last cluster shows little task-related modulation" - what criteria are they using to make this conclusion? By eye, the last cluster and cluster 1 seem to show a similar degree of modulation when locked to motion onset.

We added a new figure (Suppl Figure 2) that shows the summary of choice and coherence modulation, based on multiple linear regression analysis, for each subpopulation separately. 

Reviewer #3:

We have grouped the reviewer’s public and specific comments by content. 

First, the interpretation of the neural subpopulations' activity patterns in relation to the computational models should be clarified, as the observed patterns may not directly correspond to the specific signals predicted by the models. The authors claim that the first subpopulation of STN neurons reflects the normalization signal predicted by the model of Bogacz and Gurney (2007). However, the observed activity patterns only show choice- and coherence-dependent activity, which may represent the input to the normalization computation rather than its output. The authors should clarify this point and discuss the limitations of their interpretation. 

We agree with the reviewer that the choice- and coherence-dependent activity pattern does not sufficiently indicate a normalization computation. We interpreted such activity as satisfying a necessary condition for, and therefore consistent with, the theoretical model proposed by Bogacz and Gurney. We have reviewed the text to ensure that we never made the claim that the first subpopulation mediates the normalization.   

Second, the authors could consider using a supervised learning method to more explicitly model the pattern correlations between the three profiles. The authors used k-means clustering to identify STN subpopulations. Given the clear distinction between the three types of neural firing patterns, a supervised learning method (e.g., a generalized linear model) could be used as a more explicit encoding model to account for the pattern correlations between the three profiles.

We used two approaches to examine the different response profiles. The “random-seed” approach used non-supervised clustering to probe the functional organization of STN neurons, with no a priori assumption about how many subpopulations may be present. The “model-seed” approach is similar in spirit to what the reviewer suggested: we defined artificial vectors, akin to regressors in a generalized linear model, that showed key modulation features as predicted by previous theoretical models. We then projected the neurons’ activity profiles onto these vectors, akin to performing a regression analysis.   

Third, a neural population model could be employed to better understand how the STN population jointly contributes to decision-making dynamics. The single-neuron encoding analysis reveals mixed effects from multiple decision-related functions. To better understand how the STN population jointly contributes to the decision-making process, the authors could consider using a neural population model (e.g., Wang et al., 2023) to quantify the population dynamics.

We agree with the reviewer that a neural population model would be helpful for testing our understanding of the roles of STN. However, we believe that this is premature at the moment because we have no knowledge about how these different subpopulations interact with each other within STN, nor how they interact with other basal ganglia nuclei. We hope our results provide a foundation for future experiments that can provide more specific insights in the roles of each subpopulation, which can then be tested in a neural population model as the reviewer suggested.  

Finally, the added value of the microstimulation experiments should be more directly addressed in the Results section, as the changes in firing patterns compared to the original patterns are not clearly evident. The microstimulation results (Figure 7A) do not show significant changes in firing patterns compared to the original patterns (Figure 3B). As microstimulation is used to identify the hypothetical role of the STN beyond the correlational analysis, the authors should more directly address the added value of these experiments in the Results section.

We apologize for the confusion. The average firing rates at the top of original Figure 7A (now Figure 8A) were obtained in recordings just before microstimulation, to document which neuron subpopulation was near the stimulation electrode. We were not able to obtain recordings from the same neurons during microstimulation.  

The ordering of the three hypotheses in the Introduction (1) adjusting decision bounds, (2) computing a normalization signal, (3) implementing a nonlinear computation to improve decision bound adjustment, is inconsistent with the order in which they are addressed in the Results section (2, 1, 3). To improve clarity and readability, the authors should consider presenting the hypotheses and their corresponding results in a consistent order throughout the manuscript.

We thank the reviewer for this suggestion. We have reordered the text in Introduction to be consistent.

Reviewer #3 (Public Review):

Summary:

The manuscript by Hallam et al describes the analysis of various biomarkers in patients undergoing complement factor I supplementation treatment (PPY988 gene therapy) as part of the FOCUS Phase I/II clinical trial. The authors used validated methods (multiplexed assays and OLINK proteomics) for measuring multiple soluble complement proteins in the aqueous humour (AH) and vitreous humour (VH) of 28 patients over a series of time points, up to and including 96 weeks. Based on biomarker comparisons, the levels of FI synthesised by PPY988 were believed to be insufficient to achieve the desired level of complement inhibition. Subsequent comparative experiments showed that PPY988-delivered FI was much less efficacious than Pegceptacoplan (FDA-approved complement inhibitor under the name SYFORVE) when tested in an artificial VH matrix.

Strengths:

The manuscript is well written with data clearly presented and appropriate statistics used for the analysis itself. It's great to see data from real clinical samples that can help support future studies and therapeutic design. The identification that complement biomarker levels present in the AH do not represent the levels found in the VH is an important finding for the field, given the number of complement-targeting therapies in development and the desperate need for good biomarkers for target engagement. This study also provides a wealth of baseline complement protein measurements in both human AH and VH (and companion measurements in plasma) that will prove useful for future studies.

Weaknesses:

Perhaps the conclusions drawn regarding the lack of observed efficacy are not fully justified. The authors focus on the hypothesis that not enough FI was synthesised in these patients receiving the PPY988 gene therapy, suggesting a delivery/transduction/expression issue. But beyond rare CFI genetic variants, most genetic associations with AMD imply that it is a FI-cofactor disease. A hypothesis supported by the authors' own experiments when they supplement their artificial VH matrix with FH and achieve a significantly greater breakdown of C3b than achieved with PPY988 treatment alone. Justification around doubling FI levels driving complement turnover refers to studies conducted in blood, which has an entirely different complement protein profile than VH. In Supplemental Table 5 we see there is approx. 10-fold more FH than FI (533ug/ml vs 50ug/ml respectively) so increasing FI levels will have a direct effect. Yet in Supplemental Table 3 we see there is more FI than FH in VH (608ng/ml vs 466ng/ml respectively). Therefore, adding more FI without more co-factors would have a very limited effect. Surely this demonstrates that the study was delivering the wrong payload, i.e. FI, which hit a natural ceiling of endogenous co-factors within the eye?

eLife assessment

This important work advances our understanding of factors influencing efficacy assessments and biomarker viability for complement-directed gene therapy against age-related macular degeneration. The data presented is convincing and offers insights and teachings for the design of gene therapy and complement-targeted therapeutics in the eye and more broadly for future ocular biomarker studies.

Reviewer #1 (Public Review):

Summary:

This study analyzed biomarker data from 28 subjects with geographic atrophy (GA) in a Phase I/II clinical trial of PPY988, a subretinal AAV2 complement factor I (CFI) gene therapy, to evaluate pharmacokinetics and pharmacodynamics. Post-treatment, a 2-fold increase in the vitreous humor (VH) FI was observed, correlating with a reduction in FB breakdown product Ba but minimal changes in other complement factors. The aqueous humor (AH) was found to be an unreliable proxy for VH in assessing complement activation. In vitro assays showed that the increase in FI had a minor effect on the complement amplification loop compared to the more potent C3 inhibitor pegcetacoplan. These findings suggest that PPY988 may not provide enough FI protein to effectively modulate complement activation and slow GA progression, highlighting the need for a thorough biomarker review to determine optimal dosing in future studies.

Strengths:

This manuscript provides critical data on the efficacy of gene therapy for the eye, specifically introducing complement FI expression. It presents the results from a halted clinical trial, making sharing this data essential for understanding the outcomes of this gene therapy approach. The findings offer valuable insights and lessons for future gene therapy attempts in similar contexts.

Weaknesses:

No particular weaknesses. The study was carefully performed and limitations are discussed.

I have just some concerns about the methodology used. The authors use the MILLIPLEX assays, which allow for multiplexed detection of complement proteins and they mention extensive validation. How are the measurements with this assay correlating with gold standard methods? Is the specificity and the expected normal ranges preserved with this assay? This also stands for the Olink assay. Some of the proteins are measured by both assay and/or by standard ELISA. How do these measurements correlate?

Reviewer #2 (Public Review):

Summary:

The results presented demonstrate that AAV2-CFI gene therapy delivers long-term and marginally higher FI protein in vitreous humor that results in a concomitant reduction in the FB activation product Ba. However, the lack of clinical efficacy in the phase I/II study, possibly due to lower in vitro potency when compared to currently approved pegcetacoplan, raises important considerations for the utility of this therapeutic approach. Despite the early termination of the PPY988 clinical development program, the study achieved significant milestones, including the implementation of subretinal gene therapy delivery in older adults, complement biomarker comparison between serial vitreous humor and aqueous humor samples and vitreous humor proteomic assessment via Olink.

Strengths:

Long-term augmentation of FI protein in vitreous humor over 96 weeks and reduction of FB breakdown product Ba in vitreous humor suggests modulation of the complement system. Developed a novel in vitro assay suggesting FI's ability to reduce C3 convertase activity is weaker than pegcetacoplan and FH and may suggest a higher dose of FI will be required for clinical efficacy. Warn of the poor correlation between vitreous humor and aqueous humor biomarkers and suggest aqueous humor may not be a reliable proxy for vitreous humor with regard to complement activation/inhibition studies.

Weaknesses:

The vitrectomy required for the subretinal route of administration causes a long-term loss of total protein and may influence the interpretation of complement biomarker results even with normalization. The modified in vitro assay of complement activation suggests a several hundred-fold increase in FI protein is required to significantly affect C3a levels. Interestingly, the in vitro assay demonstrates 100% inhibition of C3a with pegcetacoplan and FH therapeutics, but only a 50% reduction with FI even at the highest concentrations tested. This observation suggests FI may not be rate-limiting for negative complement regulation under the in vitro conditions tested and potentially in the eye. It is unclear if pharmacokinetic and pharmacodynamic properties in aqueous humor and vitreous humor compartments are reliable predictors of FI level/activity after subretinal delivery AAV2-CFI gene therapy.

Reviewer #1 (Public Review):

In this manuscript by Wu et al., the authors present the high resolution cryoEM structures of the WT Kv1.2 voltage-gated potassium channel. Along with this structure, the authors have solved several structures of mutants or experimental conditions relevant to the slow inactivation process that these channels undergo and which is not yet completely understood.

One of the main findings is the determination of the structure of a mutant (W366F) that is thought to correspond to the slow inactivated state. These experiments confirm results in similar mutants in different channels from Kv1.2 that indicate that inactivation is associated with an enlarged selectivity filter.

Another interesting structure is the complex of Kv1.2 with the pore blocking toxin Dendrotoxin 1. The results shown in the revised version indicate that the mechanism of block is similar to that of related blocking-toxins, in which a lysine residue penetrates in the pore. Surprisingly, in these new structures, the bound toxin results in a pore with empty external potassium binding sites.

The quality of the structural data presented in this revised manuscript is very high and allows for unambiguous assignment of side chains. The conclusions are supported by the data. This is an important contribution that should further our understanding of voltage-dependent potassium channel gating. In the revised version, the authors have addressed my previous specific comments.

Reviewer #2 (Public Review):

Cryo_EM structures of the Kv1.2 channel in the open, inactivated, toxin complex and in Na+ are reported. The structures of the open and inactivated channels are merely confirmatory of previous reports. The structures of the dendrotoxin bound Kv1.2 and the channel in Na+ are new findings that will of interest to the general channel community.

Review of the resubmission:

I thank the authors for making the changes in their manuscript as suggested in the previous review. The changes in the figures and the additions to the text do improve the manuscript. The new findings from a further analysis of the toxin channel complex are welcome information on the mode of the binding of dendrotoxin.

Reviewer #3 (Public Review):

Wu et al. present cryo-EM structures of the potassium channel Kv1.2 in open, C-type inactivated, toxin-blocked and presumably sodium-bound states at 3.2 Å, 2.5 Å, 2.8 Å, and 2.9 Å. The work builds on a large body of structural work on Kv1.2 and related voltage-gated potassium channels. The manuscript presents a plethora of structural work, and the authors are commended on the breadth of the studies. The structural studies are well-executed. Although the findings are mostly confirmatory, they do add to the body of work on this and related channels. Notably, the authors present structures of DTx-bound Kv1.2 and of Kv1.2 in a low concentration of potassium (which may contain sodium ions bound within the selectivity filter). These two structures add considerable new information. The DTx structure has been markedly improved in the revised version and the authors arrive at well-founded conclusions regarding its mechanism of block. Overall, the manuscript is well-written, a nice addition to the field, and a crowning achievement for the Sigworth lab.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

In this manuscript by Wu et al., the authors present the high resolution cryoEM structures of the WT Kv1.2 voltagegated potassium channel. Along with this structure the authors have solved several structures of mutants or experimental conditions relevant to the slow inactivation process that these channels undergo and which is not yet completely understood. 

One of the main findings is the determination of the structure of a mutant (W366F) that is thought to correspond to the slow inactivated state. These experiments confirm results in similar mutants in different channels from Kv1.2 that indicate that inactivation is associated with an enlarged selectivity filter. 

Another interesting structure is the complex of Kv1.2 with the pore blocking toxin Dendrotoxin 1. The results shown in the revised version indicate that the mechanism of block is similar to that of related blocking-toxins, in which a lysine residue penetrates in the pore. Surprisingly, in these new structures, the bound toxin results in a pore with empty external potassium binding sites. 

The quality of the structural data presented in this revised manuscript is very high and allows for unambiguous assignment of side chains. The conclusions are supported by the data. This is an important contribution that should further our understanding of voltage-dependent potassium channel gating. In the revised version, the authors have addressed my previous specific comments, which are appended below. 

(1) In the main text's reference to Figure 2d residues W18' and S22' are mentioned but are not labeled in the insets. 

This has been fixed: line 229, p. 9.

(2) On page 8 there is a discussion of how the two remaining K+ ions in binding sites S3 and S4 prevent permeation K+ in molecular dynamics. However, in Shaker, inactivated W434F channels can sporadically allow K+ permeation with normal single-channel conductance but very reduced open times and open probability at not very high voltages. 

This is noted in the discussion Lines 497-500, p. 18

(3) The structures of WT in the absence of K+ shows a narrower selectivity filter, however Figure 4 does not convey this finding. In fact, the structure in Figure 4B is constructed in such an angle that it looks as if the carbonyl distances are increased, perhaps this should be fixed. Also, it is not clear how the distances between carbonyls given in the text on page 12 are measured. Is it between adjacent or kitty-corner subunits? 

We have changed Fig. 4B to show the same view as in Fig. 4A. In the legend we explain that opposing subunits are shown. We no longer give distances, in view of the lack of detectable carbonyl densities.

(4) It would be really interesting to know the authors opinion on the driving forces behind slow inactivation. For example, potassium flux seems to be necessary for channels to inactivate, which might indicate a local conformational change is the trigger for the main twisting events proposed here. 

We address this in the Discussion, line 506-523, pp. 18-19.

Reviewer #2 (Public Review): 

Cryo_EM structures of the Kv1.2 channel in the open, inactivated, toxin complex and in Na+ are reported. The structures of the open and inactivated channels are merely confirmatory of previous reports. The structures of the dendrotoxin bound Kv1.2 and the channel in Na+ are new findings that will of interest to the general channel community. 

Review of the resubmission: 

I thank the authors for making the changes in their manuscript as suggested in the previous review. The changes in the figures and the additions to the text do improve the manuscript. The new findings from a further analysis of the toxin channel complex are welcome information on the mode of the binding of dendrotoxin. 

A few minor concerns: 

(1) Line 93-96, 352: I am not sure as to what is it the authors are referring to when they say NaK2P. It is either NaK or NaK2K. I don't think that it has been shown in the reference suggested that either of these channels change conformation based on the K+ concentration. Please check if there is a mistake and that the Nichols et. al. reference is what is being referred to. 

Thank you for noticing the error. We meant NaK2K and we have changed this throughout.

(2) Line 365: In the study by Cabral et. al., Rb+ ions were observed by crystallography in the S1, S3 and S4 site, not the S2 site. Please correct. 

Thank you. We have re-written this section, lines 364-381, pp. 13-14.

Reviewer #3 (Public Review): 

Wu et al. present cryo-EM structures of the potassium channel Kv1.2 in open, C-type inactivated, toxin-blocked and presumably sodium-bound states at 3.2 Å, 2.5 Å, 2.8 Å, and 2.9 Å. The work builds on a large body of structural work on Kv1.2 and related voltage-gated potassium channels. The manuscript presents a plethora of structural work, and the authors are commended on the breadth of the studies. The structural studies are well-executed. Although the findings are mostly confirmatory, they do add to the body of work on this and related channels. Notably, the authors present structures of DTx-bound Kv1.2 and of Kv1.2 in a low concentration of potassium (which may contain sodium ions bound within the selectivity filter). These two structures add considerable new information. The DTx structure has been markedly improved in the revised version and the authors arrive at well-founded conclusions regarding its mechanism of block. Regarding the Na+ structure, the authors claim that the structure with sodium has "zero" potassium - I caution them to make this claim. It is likely that some K+ persists in their sample and that some of the density in the "zero potassium" structure may be due to K+ rather than Na+. This can be clarified by revisions to the text and discussion. I do not think that any additional experiments are needed. Overall, the manuscript is well-written, a nice addition to the field, and a crowning achievement for the Sigworth lab. 

Most of this reviewer's initial comments have been addressed in the revised manuscript. Some comments remain that could be addressed by revisions of the text. 

Specific comments on the revised version: 

Quotations indicate text in the manuscript. 

(1) "While the VSD helices in Kv1.2s and the inactivated Kv1.2s-W17'F superimpose very well at the top (including the S4-S5 interface described above), there is a general twist of the helix bundle that yields an overall rotation of about 3o at the bottom of the VSD." 

Comment: This seemed a bit confusing. I assume the authors aligned the complete structures - the differences they indicate seem to be slight VSD repositioning relative to the pore rather than differences between the VSD conformations themselves. The authors may wish to clarify. As they point out in the subsequent paragraph, the VSDs are known to be loosely associated with the pore. 

We aligned the VSDs alone, and it is a twist of the VSD helix bundle.

This is now clarified in lines 269-273, p. 10.

(2) Comment: The modeling of DTx into the density is a major improvement in the revision. Figure 3 displays some interactions between the toxin and Kv1.2 - additional side views of the toxin and the channel might allow the reader to appreciate the interactions more fully. The overall fit of the toxin structure into the density is somewhat difficult to assess from the figure. (The authors might consider using ChimeraX to display density and model in this figure.) 

We have added new panels, and stereo pairs, to Figure 3.

(3) "We obtained the structure of Kv1.2s in a zero K+ solution, with all potassium replaced with sodium, and were surprised to find that it is little changed from the K+ bound structure, with an essentially identical selectivity filter conformation (Figure 4B and Figure 4-figure supplement 1)." 

Comment: It should be noted in the manuscript that K+ and Na+ ions cannot be distinguished by the cryo-EM studies - the densities are indistinguishable. The authors are inferring that the observed density corresponds to Na+ because the protein was exchanged from K+ into Na+ on a gel filtration (SEC) column. It is likely that a small amount of K+ remains in the protein sample following SEC. I caution the authors to claim that there is zero K+ in solution without measuring the K+ content of the protein sample. Additionally, it should be considered that K+ may be present in the blotting paper used for cryo-EM grid preparation (our laboratory has noted, for example, a substantial amount of Ca2+ in blotting paper). The affinity of Kv1.2 for K+ has not been determined, to my knowledge - the authors note in the Discussion that the Shaker channel has "tight" binding for K+. It seems possible that some portion of the density in the selectivity filter could be due to residual K+. This caveat should be clearly stated in the main text and discussion. More extensive exchange into Na+, such as performing the entire protein purification in NaCl, or by dialysis (as performed for obtaining the structure of KcsA in low K+ by Y. Zhou et al. & Mackinnon 2001), would provide more convincing removal of K+, but I suspect that the Kv1.2 protein would not have sufficient biochemical stability without K+ to endure this treatment. One might argue that reduced biochemical stability in NaCl could be an indication that there was a meaningful amount of K+ in the final sample used for cryo-EM (or in the particles that were selected to yield the final high-resolution structure).

We now explain in the Methods section, in more detail the steps taken to avoid any residual Na+ contamination during purification, lines 683-687, pp. 24-25. We have changed the text to point out that the ion species cannot be distinguished in the maps, and note results in NaK2K and KcsA (lines 368-381, pp. 13-14).

We note that the same procedures to remove K+ were used for the Kv1.2sW17’F structure (line 385, p. 14). We qualify the ion replacement to say that Na+ replaces “essentially” all K+ (line 607, p. 21).

(4) Referring to the structure obtained in NaCl: "The ion occupancy is also similar, and we presume that Kv1.2 is a conducting channel in sodium solution." 

Comment: Stating that "Kv1.2 is a conducting channel in sodium solution" and implying that conduction of Na+ is achieved by an analogous distribution of ion binding sites as observed for K+ are strong statements to make - and not justified by the experiments provided. Electrophysiology would be required to demonstrate that the channel conducts sodium in the absence of K+. More complete ionic exchange, better control of the ionic conditions (Na+ vs K+), and affinity measurements for K+ would be needed to determine the distribution of Na+ in the filter (as mentioned above). At minimum, the authors should revise and clarify what the intended meaning of the statement "we presume that Kv1.2 is a conducting channel in sodium solution". As mentioned above, it seems possible/likely that a portion of the density in the filter may be due to K+. 

We now present a more detailed argument (lines 376 to 381, pp. 13-14.)

Recommendations for the authors: 

Reviewing Editor: 

After consultation, the reviewers agree that, although the authors have answered most of the comments raised in the previous review, there remains a concern about the structure obtained in the presence if Na. Given that Kv1.2 is more reluctant to slow inactivation, the conducting structure in Na+ could be due to this fact or that it really has higher affinity for K+ than Na+. In the presence of even a small contamination by K+, this ion could thus occupy the selectivity filter, resulting in an open conformation. The authors should clearly state the steps taken to ensure no contamination by K+. It is also possible that indeed the open structure occurs even in the presence of Na+ in the selectivity filter. This should be also discussed, given that this has been observed in other potassium channel structures. 

Reviewer #1 (Recommendations For The Authors): 

In this revised version of the manuscript, the authors have adequately addressed my previous points and improved the clarity and readability of the manuscript. This is a compelling work that shows inactivated structures if the Kv1.2 potassium channel, especially interesting is a structure in the absence of extracellular potassium ions, that can help understand how a reduction in the availability of these ions speed up entrance into the inactivated state in these ion channels. 

I would just recommend that in the absence of functional data (current recordings) when potassium is removed, the authors just use caution in ascribing this structure to an inactivated state. Also, it should be mentioned that the observed ion densities observed in the pore cannot unambiguously be identified as sodium ions. 

Reviewer #3 (Recommendations For The Authors): 

(1)  "The nearby Leu9 is also important as its substitution by alanine also decreases affinity 1000-fold, but we observe no contacts between this residue and residues of the Kv1.2s channel." 

Comment: It seems early in the text to mention the potential interaction of Leu9 to the channel structure. The authors may wish to discuss Leu9 later in the manuscript - a figure showing the location of Leu9 would strengthen the statement. Any hypothesis on why mutation of it has such a profound effect? 

Add a figure panel showing Leu9 position.

We have rewritten the text as suggested, and have identified Leu9 in several panels of Fig. 3.

(2)  "The X-ray structure of a-DTX (Figure 3A)" 

Comment: The authors may wish to cite a reference to this X-ray structure. 

We now cite Skarzynski (1992) on line 321, p. 12.

eLife assessment

This paper investigates how isoform II of transcription factor RUNX2 promotes cell survival and proliferation in oral squamous cell carcinoma cell lines. The authors used gain and loss of function techniques to provide incomplete evidence showing that RUNX2 isoform silencing led to cell death via several mechanisms including ferroptosis that was partially suppressed through RUNX2 regulation of PRDX2 expression. The study provides useful insight into the underlying mechanism by which RUNX2 acts in oral squamous cell carcinoma, but the conclusions of the authors should be revised to acknowledge that ferroptosis is not the only cause of cell death.

Reviewer #1 (Public Review):

Summary:<br /> In this paper, authors investigated the role of RUNT-related transcription factor 2 (RUNX2) in oral squamous carcinoma (OSCC) growth and resistance to ferroptosis. They found that RUNX2 suppresses ferroptosis through transcriptional regulation of peroxiredoxin-2. They further explored the upstream positive regulator of RUNX2, HOXA10 and found that HOXA10/RUNX2/PRDX2 axis protects OSCC from ferroptosis.

Strengths:<br /> The study is well designed and provides a novel mechanism of HOXA10/RUNX2/PRDX2 control of ferroptosis in OSCC.

Weaknesses:

According to the data presented in (Figure 2F, Figure 3Fand G, Figure 5D and Figure 6E and F), apoptosis seems to be affected in the same amount as ferroptosis by HOXA10/RUNX2/PRDX2 axis, which raises questions on the authors' specific focus on ferroptosis in this study. Reasonably, authors should adapt the title and the abstract in a way that recapitulates the whole data, which is HOXA10/RUNX2/PRDX2 axis control of cell death, including ferroptosis and apoptosis in OSCC.

Comments:

- In the description of the result section related to Figure 3E, the author wrote "In addition, we found that isoform II-knockdown induced shrunken mitochondria with vanished cristae with transmission electron microscopy (Figure 3E). These results suggest that RUNX2 isoform II may suppress ferroptosis." The interpretation provided here is not clear to the reviewer. How shrunken mitochondria and vanished cristae can be linked to ferroptosis?<br /> - The electron microscopy images show more elongated mitochondria in the RUNX2 isoform II-KO cells than in RUNX2 isoform II positive cells, which might result from the fusion of mitochondria. These images should completed with a fluorescent mitochondria staining of these cells.<br /> - What is the oxygen consumption rate in RUNX2 KO cells?<br /> - The increase in cell proliferation after RUNX2 overexpression in Figure 2A is not convincing, is there any differences in their migration or invasion capacity?<br /> - The in vivo study shows 50% reduction in primary tumor growth after RUNX2 inhibition by shRNA in CAL 27 xenografts, but only one shRNA is shown. Is this one shRNA clone? At least 2 shRNA clones should be used.<br /> - Apoptosis and necroptosis seem to be affected in the same amount as ferroptosis by HOXA10/RUNX2/PRDX2 axis. This is evident from experiments in Figure 3E, F and from Figure 6E, F and Figure 3G. Either Fer-1, Z-VAD,or Nec-1 used alone, were not able to fully restore cell proliferation to control cell level, which implies an additive effect of ferroptosis, apoptosis and necrosis. The author should verify potential additive or synergistic effect of the combination of Fer-1 and Z-VAD in these assays after si-RUNX2 in Figure 3 F and G and after si-HOX assays.<br /> - What is the effect of PRDX2 or HOXA10 depletion on tumor growth?<br /> - What is the clinical relevance of HOXA10 in OSCC patients?

Reviewing #2 (Public Review):

This paper reports the role of the Isoform II of RUNX2 in activating PRDX2 expression to suppress ferroptosis in oral squamous cell carcinoma (OSCC).<br /> The following major issues should be addressed.

A major postulate of this study is the specific role of RUNX2 isoform II compared to isoform I.

Figure 1F shows association between patient survival and Iso II expression, but nothing is shown for Iso I, this should be added, in addition the number of patients at risk in each category should be shown.<br /> The authors test Iso I and Iso II overexpression in CAL27 or SCC-9 model cell lines. In Fig. 2A in CAL27, the overexpression of Iso II is much stronger than Iso I so it seems premature to draw any conclusions. More importantly, however, no Iso I silencing is shown in either of the cell lines nor the xenografted tumours. This is absolutely essential for the authors hypothesis and should be tested using shRNA in cells and xenografted tumours.

A major conclusion of this study is that Iso II expression suppresses ferroptosis. To support this idea, the authors use the inhibitor Ferrostatin-1 (Fer-1). While Fer-1 typically does not lead to a 100% rescue, here the effect is only marginal and as shown in Figures 3F and G only marginally better than Z-VAD or Necrostatin 1. These data do not support the idea that the major cause of cell death is ferroptosis. Instead, Iso II silencing leads to cell death through different pathways. The authors should acknowledge this and rephrase the conclusion of the paper accordingly.<br /> Moreover, the authors consistently confound cell proliferation with cell death.

In Fig. 4A the authors investigate GPX1 expression, whereas GPX4 is often the key ferroprosis regulator, this has to be tested. This is important as the authors also test the effect of the GPX4 inhibitor RSL3, however, the authors do not determine IC50 values of the different cell lines with or without Iso II overexpression or silencing or compared to other RSL3 sensitive or resistant cells. Without this information, no conclusions can be drawn.

In summary, while the authors show that RUNX2 Iso II expression enhances cell survival, the idea that cell death is principally via ferroptosis is not fully established by the data. The authors should modify their conclusions accordingly.

eLife assessment

Mark and colleagues developed and validated a valuable method for examining subspace generalization in fMRI data and applied it to understand whether the entorhinal cortex uses abstract representations that generalize across different environments with the same structure. Evidence supporting the empirical findings - which show abstract entorhinal representations of hexagonal associative structures across different stimulus sets - is solid but could be further supported through additional analyses, discussion, and clarifications.

Reviewer #1 (Public review):

Summary:

This study develops and validates a neural subspace similarity analysis for testing whether neural representations of graph structures generalize across graph size and stimulus sets. The authors show the method works in rat grid and place cell data, finding that grid but not place cells generalize across different environments, as expected. The authors then perform additional analyses and simulations to show that this method should also work on fMRI data. Finally, the authors test their method on fMRI responses from the entorhinal cortex (EC) in a task that involves graphs that vary in size (and stimulus set) and statistical structure (hexagonal and community). They find neural representations of stimulus sets in lateral occipital complex (LOC) generalize across statistical structure and that EC activity generalizes across stimulus sets/graph size, but only for the hexagonal structures.

Strengths:

(1) The overall topic is very interesting and timely and the manuscript is well-written.

(2) The method is clever and powerful. It could be important for future research testing whether neural representations are aligned across problems with different state manifestations.

(3) The findings provide new insights into generalizable neural representations of abstract task states in the entorhinal cortex.

Weaknesses:

(1) The manuscript would benefit from improving the figures. Moreover, the clarity could be strengthened by including conceptual/schematic figures illustrating the logic and steps of the method early in the paper. This could be combined with an illustration of the remapping properties of grid and place cells and how the method captures these properties.

(2) Hexagonal and community structures appear to be confounded by training order. All subjects learned the hexagonal graph always before the community graph. As such, any differences between the two graphs could thus be explained (in theory) by order effects (although this is practically unlikely). However, given community and hexagonal structures shared the same stimuli, it is possible that subjects had to find ways to represent the community structures separately from the hexagonal structures. This could potentially explain why the authors did not find generalizations across graph sizes for community structures.

(3) The authors include the results from a searchlight analysis to show the specificity of the effects of EC. A better way to show specificity would be to test for a double dissociation between the visual and structural contrast in two independently defined regions (e.g., anatomical ROIs of LOC and EC).

(4) Subjects had more experience with the hexagonal and community structures before and during fMRI scanning. This is another confound, and possible reason why there was no generalization across stimulus sets for the community structure.

Reviewer #2 (Public review):

Summary:

Mark and colleagues test the hypothesis that entorhinal cortical representations may contain abstract structural information that facilitates generalization across structurally similar contexts. To do so, they use a method called "subspace generalization" designed to measure abstraction of representations across different settings. The authors validate the method using hippocampal place cells and entorhinal grid cells recorded in a spatial task, then perform simulations that support that it might be useful in aggregated responses such as those measured with fMRI. Then the method is applied to fMRI data that required participants to learn relationships between images in one of two structural motifs (hexagonal grids versus community structure). They show that the BOLD signal within an entorhinal ROI shows increased measures of subspace generalization across different tasks with the same hexagonal structure (as compared to tasks with different structures) but that there was no evidence for the complementary result (ie. increased generalization across tasks that share community structure, as compared to those with different structures). Taken together, this manuscript describes and validates a method for identifying fMRI representations that generalize across conditions and applies it to reveal entorhinal representations that emerge across specific shared structural conditions.

Strengths:

I found this paper interesting both in terms of its methods and its motivating questions. The question asked is novel and the methods employed are new - and I believe this is the first time that they have been applied to fMRI data. I also found the iterative validation of the methodology to be interesting and important - showing persuasively that the method could detect a target representation - even in the face of a random combination of tuning and with the addition of noise, both being major hurdles to investigating representations using fMRI.

Weaknesses:

In part because of the thorough validation procedures, the paper came across to me as a bit of a hybrid between a methods paper and an empirical one. However, I have some concerns, both on the methods development/validation side, and on the empirical application side, which I believe limit what one can take away from the studies performed.

Regarding the methods side, while I can appreciate that the authors show how the subspace generalization method "could" identify representations of theoretical interest, I felt like there was a noticeable lack of characterization of the specificity of the method. Based on the main equation in the results section of the paper, it seems like the primary measure used here would be sensitive to overall firing rates/voxel activations, variance within specific neurons/voxels, and overall levels of correlation among neurons/voxels. While I believe that reasonable pre-processing strategies could deal with the first two potential issues, the third seems a bit more problematic - as obligate correlations among neurons/voxels surely exist in the brain and persist across context boundaries that are not achieving any sort of generalization (for example neurons that receive common input, or voxels that share spatial noise). The comparative approach (ie. computing difference in the measure across different comparison conditions) helps to mitigate this concern to some degree - but not completely - since if one of the conditions pushes activity into strongly spatially correlated dimensions, as would be expected if univariate activations were responsive to the conditions, then you'd expect generalization (driven by shared univariate activation of many voxels) to be specific to that set of conditions. A second issue in terms of the method is that there is no comparison to simpler available methods. For example, given the aims of the paper, and the introduction of the method, I would have expected the authors to take the Neuron-by-Neuron correlation matrices for two conditions of interest, and examine how similar they are to one another, for example by correlating their lower triangle elements. Presumably, this method would pick up on most of the same things - although it would notably avoid interpreting high overall correlations as "generalization" - and perhaps paint a clearer picture of exactly what aspects of correlation structure are shared. Would this method pick up on the same things shown here? Is there a reason to use one method over the other?

Regarding the fMRI empirical results, I have several concerns, some of which relate to concerns with the method itself described above. First, the spatial correlation patterns in fMRI data tend to be broad and will differ across conditions depending on variability in univariate responses (ie. if a condition contains some trials that evoke large univariate activations and others that evoke small univariate activations in the region). Are the eigenvectors that are shared across conditions capturing spatial patterns in voxel activations? Or, related to another concern with the method, are they capturing changing correlations across the entire set of voxels going into the analysis? As you might expect if the dynamic range of activations in the region is larger in one condition than the other? My second concern is, beyond the specificity of the results, they provide only modest evidence for the key claims in the paper. The authors show a statistically significant result in the Entorhinal Cortex in one out of two conditions that they hypothesized they would see it. However, the effect is not particularly large. There is currently no examination of what the actual eigenvectors that transfer are doing/look like/are representing, nor how the degree of subspace generalization in EC may relate to individual differences in behavior, making it hard to assess the functional role of the relationship. So, at the end of the day, while the methods developed are interesting and potentially useful, I found the contributions to our understanding of EC representations to be somewhat limited.

Reviewer #3 (Public review):

Summary:

The article explores the brain's ability to generalize information, with a specific focus on the entorhinal cortex (EC) and its role in learning and representing structural regularities that define relationships between entities in networks. The research provides empirical support for the longstanding theoretical and computational neuroscience hypothesis that the EC is crucial for structure generalization. It demonstrates that EC codes can generalize across non-spatial tasks that share common structural regularities, regardless of the similarity of sensory stimuli and network size.

Strengths:

(1) Empirical Support: The study provides strong empirical evidence for the theoretical and computational neuroscience argument about the EC's role in structure generalization.

(2) Novel Approach: The research uses an innovative methodology and applies the same methods to three independent data sets, enhancing the robustness and reliability of the findings.

(3) Controlled Analysis: The results are robust against well-controlled data and/or permutations.

(4) Generalizability: By integrating data from different sources, the study offers a comprehensive understanding of the EC's role, strengthening the overall evidence supporting structural generalization across different task environments.

Weaknesses:

A potential criticism might arise from the fact that the authors applied innovative methods originally used in animal electrophysiology data (Samborska et al., 2022) to noisy fMRI signals. While this is a valid point, it is noteworthy that the authors provide robust simulations suggesting that the generalization properties in EC representations can be detected even in low-resolution, noisy data under biologically plausible assumptions. I believe this is actually an advantage of the study, as it demonstrates the extent to which we can explore how the brain generalizes structural knowledge across different task environments in humans using fMRI. This is crucial for addressing the brain's ability in non-spatial abstract tasks, which are difficult to test in animal models.

While focusing on the role of the EC, this study does not extensively address whether other brain areas known to contain grid cells, such as the mPFC and PCC, also exhibit generalizable properties. Additionally, it remains unclear whether the EC encodes unique properties that differ from those of other systems. As the authors noted in the discussion, I believe this is an important question for future research.

eLife assessment

In this important study, the authors have partially revealed the mechanism behind lip thickening in cichlid fishes, which has evolved independently across three lakes in Africa. To explore this phenomenon, the authors utilized histological comparison, proteomics, and transcriptomics, all of which are well suited for their objectives. With convincing evidence, this contribution holds significant value for the field.

Reviewer #1 (Public Review):

Summary:

Machii et al. reported a possible molecular mechanism underlying the parallel evolution of lip hypertrophy in African cichlids. The multifaceted approach taken in this manuscript is highly valued, as it uses histology, proteomics, and transcriptomics to reveal how phylogenetically distinct thick-lips have evolved in parallel. Findings from histology and proteomics connected to wnt signaling through the transcriptome are very exciting.

Strengths:

There is consistency between the results and it is possible to make a strong argument from the results.

Weaknesses:

The authors do not discuss based on genomic information; the genomes of the cichlids from the three lakes have been decoded and are therefore available. However, indeed, the species in Lake Tanganyika and Lake Malawi/Victoria are genetically distant from each other, so a comparative genome analysis would not have yielded the results presented here. I recommend adding such a discussion to the Discussion.

Reviewer #2 (Public Review):

I have carefully reviewed the manuscript titled "Pronounced expression of extracellular matrix proteoglycans regulated by Ant pathway underlies the parallel evolution of lip hypertrophy in East African cichlids." I commend the authors for their work on elucidating the mechanism underlying lip thickening that has evolved in parallel across three lakes in Africa.

The use of histological comparison, proteomics, and transcriptomics methods to investigate this phenomenon is commendable and adds depth to the study. The findings indicate that the overexpression of proteoglycans is the cause of lip thickening and provides valuable insights into the evolutionary process.

I found the writing style to be clear and the explanations provided are easy to understand. Overall, I did not identify any significant issues with the manuscript.

eLife assessment

This study presents an interesting mechanism for the regulation of RNA levels, establishing an important regulatory connection between protein arginine methyltransferase 1 and the splicing factor SFPQ. While these findings have theoretical implications beyond a single field, the evidence is incomplete, with only partial support for the main claims.

Reviewer #1 (Public review):

The central finding of the current manuscript is that embryonic ablation of PRMT1 results in a craniofacial phenotype that is primarily linked to downstream intron splicing defects. This manuscript is one of several to underscore the relative importance of intron splicing to gene expression regulation during development, and moreover, to recapitulate splicing-related craniofacial defects. Specifically, authors introduce a regulatory axis consisting of PRMT1-SFPQ that directs mechanisms of long intron retention. This finding represents a significant contribution to our understanding of splicing regulation, in the sense that it highlights the regulatory impact that post-translational modification of splicing-related proteins can have on intron processing. Further, it emphasizes the importance of extending the study of splicing regulation beyond core components of the spliceosome, to include their upstream regulators as well.

The significance of neural crest cells in the development of craniofacial structures has long been considered a major contributor to developmental phenotypes. This specific symptomology is heavily associated with spliceosomopathies, wherein disruption of spliceosome components is the primary mechanism of disease pathogenesis. Thus, the PRMT1 associated phenotype is noteworthy. The role of PRMT1 in methylating downstream splicing factors introduces a new avenue of research focused on the mechanisms of spliceosome component activation and their effects on splicing. The strength of the current study lies in their establishing the molecular mechanism through which PRMT1 could alter craniofacial development through regulation of the transcriptome, but the data presented to support the claim that a PRMT1-SFPQ axis directly regulates intron retention of the relevant gene networks should be robust and with multiple forms of clear validation. For example, elevated intron retention findings are based on the intron retention index, and according to the manuscript, are assessed considering the relative expression of exons and introns from a given transcript. However, delineating between intron retention and other forms of alternative splicing (i.e., cryptic splice site recognition) requires a more comprehensive consideration of the intron splicing defects that could be represented in data. A certain threshold of intron read coverage (i.e., the percent of an intron that is covered by mapped reads) is needed to ascertain if those that are proximal to exons could represent alternative introns ends rather than full intron retention events. In other words, intron retention is a type of alternative splicing that can be difficult to analyze in isolation given the confounding influence of cryptic splicing and cryptic exon inclusion. If other forms of alternative splicing were assessed and not detected, more confident retention calls can be made.

While data presented to support the PRMT1-SFPQ activation axis is quite compelling, that this is directly responsible for the elevated intron retention remains enigmatic. First, in characterizing their PRMT1 knockout model, it is unclear whether the elevated intron retention events directly correspond to downregulated genes. Moreover, intron splicing is a well-documented node for gene regulation during embryogenesis and in other proliferation models, and craniofacial defects are known to be associated with 'spliceosomopathies'. However, reproduction of this phenotype does not suggest that the targets of interest are inherently splicing factors, and a more robust assessment is needed to determine the exact nature of alternative splicing in this system. Because there are several known splicing factors downstream of PRMT1 and presented in the supplemental data, the specific attribution of retention to SFPQ would be additionally served by separating its splicing footprint from that of other factors that are primed to cause alternative splicing.

Clarifying the relationship between SFPQ and splicing regulation is important given that the observed splicing defects are incongruous with published data presented by Takeuchi et al., (2018) regarding SFPQ control of neuronal apoptosis in mice. In this system, SFPQ was more specifically attributed to the regulation of transcription elongation over long introns and its knockout did not result in significant splicing changes. Thus, to establish the specificity for the SFPQ in regulating these retention events, authors would need to show that the same phenotype is not achieved by mis-regulation of other splicing factors. That the authors chose SFPQ based on its binding profile is understandable but potentially confounding given its mechanism of action in transcription of long introns (Takeuchi 2018). Because mechanisms and rates of transcription can influence splicing and exon definition interactions, the role of SFPQ as a transcription elongation factor versus a splicing factor is inadequately disentangled by authors.

Reviewer #2 (Public review):

Summary:<br /> The manuscript by Lima et al examines the role of Prmt1 and SFPQ in craniofacial development. Specifically, the authors test the idea that Prmt1 directly methylates specific proteins that results in intron retention in matrix proteins. The protein SFPQ is methylated by Prmt1 and functions downstream to mediate Prmt1 activity. The genes with retained introns activate the NMD pathway to reduce the RNA levels. This paper describes an interesting mechanism for the regulation of RNA levels during development.

Strengths:<br /> The phenotypes support what the authors claim that Prmt1 is involved in craniofacial development and splicing. The use of state-of-the-art sequencing to determine the specific genes that have intron retention and changes in gene expression is a strength.

Weaknesses:<br /> Some of the data seems to contradict the conclusions. And it is unclear how direct the relationships are between Prmt1 and SFPQ.

eLife assessment

This important study shows how a combination of the latest generation of Oxford Nanopore Technology long reads with state-of-the art variant callers enables bacterial variant discovery at an accuracy that matches or exceeds the current "gold standard" with short reads. The work thus heralds a new era, in which Illumina short-read sequencing no longer rules supreme. While the inclusion of a larger number of reference genomes would have enabled an even more fine-grained analysis, the evidence as it is supports the claims of the authors convincingly. The work will be of interest to anyone performing sequencing for outbreak investigations, bacterial epidemiology, or similar studies.

Reviewer #2 (Public review):

Summary:

Hall et al describe the superiority of ONT sequencing and deep learning-based variant callers to deliver higher SNP and Indel accuracy compared to previous gold-standard Illumina short-read sequencing. Furthermore, they provide recommendations for read sequencing depth and computational requirements when performing variant calling.

Strengths:

The study describes compelling data showing ONT superiority when using deep learning-based variant callers, such as Clair3, compared to Illumina sequencing. This challenges the paradigm that Illumina sequencing is the gold standard for variant calling in bacterial genomes. The authors provide evidence that homopolymeric regions, a systematic and problematic issue with ONT data, are no longer a concern in ONT sequencing.

Weaknesses:

The study is limited in the number of samples included, even though it covers different species with divergent genome sequences, likely covering major evolutionary changes. The methods section could be more detailed. A structural variation analysis would be an interesting next step.

Reviewer #3 (Public review):

Hall et al. benchmarked different variant calling methods on Nanopore reads of bacterial samples and compared the performance of Nanopore to short reads produced with Illumina sequencing. To establish a common ground for comparison, the authors first generated a variant truthset for each sample and then projected this set to the reference sequence of the sample to obtain a mutated reference. Subsequently, Hall et al. called SNPs and small indels using commonly used deep learning and conventional variant callers and compared the precision and accuracy from reads produced with simplex and duplex Nanopore sequencing to Illumina data. The authors did not investigate large structural variation, which is a major limitation of the current manuscript. It will be very interesting to see a follow-up study covering this much more challenging type of variation.

In their comprehensive comparison of SNPs and small indels, the authors observed superior performance of deep learning over conventional variant callers when Nanopore reads were basecalled with the most accurate (but also computationally very expensive) model, even exceeding Illumina in some cases. Not surprisingly, Nanopore underperformed compared to Illumina when basecalled with the fastest (but computationally much less demanding) method with the lowest accuracy. The authors then investigated the surprisingly higher performance of Nanopore data in some cases and identified lower recall with Illumina short read data, particularly from repetitive regions and regions with high variant density, as the driver. Combining the most accurate Nanopore basecalling method with a deep learning variant caller resulted in low error rates in homopolymer regions, similar to Illumina data. This is remarkable, as homopolymer regions are (or, were) traditionally challenging for Nanopore sequencing.

Lastly, Hall et al. provided useful information on the required Nanopore read depth, which is surprisingly low, and the computational resources for variant calling with deep learning callers. With that, the authors established a new state-of-the-art for Nanopore-only variant calling on bacterial sequencing data. Most likely these findings will be transferred to other organisms as well or at least provide a proof-of-concept that can be built upon.

As the authors mention multiple times throughout the manuscript, Nanopore can provide sequencing data in nearly real-time and in remote regions, therefore opening up a ton of new possibilities, for example for infectious disease surveillance. In these scenarios, computational resources can be very limited. The highest-performing variant calling method, as established in this study, requires the computationally very expensive sup and/or duplex nanopore basecalling, while the least computationally demanding basecalling method underperforms. To comprehensively guide users through the computational resources required for basecalling and variant calling, the authors provide runtime benchmarks assuming GPU access.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors assess the accuracy of short variant calling (SNPs and indels) in bacterial genomes using Oxford Nanopore reads generated on R10.4 flow cells from a very similar genome (99.5% ANI), examining the impact of variant caller choice (three traditional variant callers: bcftools, freebayes, and longshot, and three deep learning based variant callers: clair3, deep variant, and nano caller), base calling model (fast, hac and sup) and read depth (using both simplex and duplex reads).

Strengths:

Given the stated goal (analysis of variant calling for reads drawn from genomes very similar to the reference), the analysis is largely complete and results are compelling. The authors make the code and data used in their analysis available for re-use using current best practices (a computational workflow and data archived in INSDC databases or Zenodo as appropriate).

Weaknesses:

While the medaka variant caller is now deprecated for diploid calling, it is still widely used for haploid variant calling and should at least be mentioned (even if the mention is only to explain its exclusion from the analysis). 

We have now added Medaka haploid caller to the benchmark. It performs quite well overall (better than the traditional methods), but not as good as Clair3 or DeepVariant.

Appraisal:

The experiments the authors engaged in are well structured and the results are convincing. I expect that these results will be incorporated into "best practice" bacterial variant calling workflows in the future. 

Thank you for the positive appraisal.

Reviewer #2 (Public Review):

Summary:

Hall et al describe the superiority of ONT sequencing and deep learning-based variant callers to deliver higher SNP and Indel accuracy compared to previous gold-standard Illumina short-read sequencing. Furthermore, they provide recommendations for read sequencing depth and computational requirements when performing variant calling.

Strengths:

The study describes compelling data showing ONT superiority when using deep learning-based variant callers, such as Clair3, compared to Illumina sequencing. This challenges the paradigm that Illumina sequencing is the gold standard for variant calling in bacterial genomes. The authors provide evidence that homopolymeric regions, a systematic and problematic issue with ONT data, are no longer a concern in ONT sequencing.

Weaknesses:

(1) The inclusion of a larger number of reference genomes would have strengthened the study to accommodate larger variability (a limitation mentioned by the authors). 

Our strategic selection of 14 genomes—spanning a variety of bacterial genera and species, diverse GC content, and both gram-negative and gram-positive species (including M. tuberculosis, which is neither)—was designed to robustly address potential variability in our results. Moreover, all our genome assemblies underwent rigorous manual inspection as the quality of the true genome sequences is the foundation this research is built upon. Given this, the fundamental conclusions regarding the accuracy of variant calls would likely remain unchanged with the addition of more genomes.  However, we do acknowledge that a substantially larger sample size, which is beyond the scope of this study, would enable more fine-grained analysis of species differences in error rates.

(2) In Figure 2, there are clearly one or two samples that perform worse than others in all combinations (are always below the box plots). No information about species-specific variant calls is provided by the authors but one would like to know if those are recurrently associated with one or two species. Species-specific recommendations could also help the scientific community to choose the best sequencing/variant calling approaches.

Thank you for highlighting this observation. The precision, recall, and F1 scores for each sample and condition can be found in Supplementary Table S4.

Upon investigation of the outliers in Figure 2 we discovered three things. First, there was a parameter in Longshot we were using that automatically capped coverage and lead to a number of false negatives, leading to its outlier. This has now been rectified and the figure is updated accordingly. Second, the outlier in the simplex sup SNP panel (top left) was the same E. coli sample for most variant callers (though Medaka had no issues). The reasoning for this was a variant dense repetitive region. We have added an in-depth explanation of this, along with figures illustrating the issue in Supplementary Section S2, with a brief statement in the main text. Third, the outlier in the duplex sup SNP panel (top right) is due to a very low (duplex) depth sample. This has also been added briefly to the main text and fully in Section S2.

We have now included a species-segregated version of Figure 2 (Suppl. Figures S5-7) for Clair3 with the sup model (best performer) for a clearer interpretation of how each species performs.

(3) The authors support that a read depth of 10x is sufficient to achieve variant calls that match or exceed Illumina sequencing. However, the standard here should be the optimal discriminatory power for clinical and public health utility (namely outbreak analysis). In such scenarios, the highest discriminatory power is always desirable and as such an F1 score, Recall and Precision that is as close to 100% as possible should be maintained (which changes the minimum read sequencing depth to at least 25x, which is the inflection point).

We agree that the highest discriminatory power is always desirable for clinical or public health applications. In which case, 25x is probably a better minimum recommendation. However, we are also aware that there are resource-limited settings where parity with Illumina is sufficient. In these cases, 10x depth from ONT would provide enough data.

The manuscript previously emphasised the latter scenario, but we have revised the text (Discussion) to clearly recommend 25x depth as a conservative aim in settings where resources are not a constraint, ensuring the highest possible discriminatory power.

(4) The sequencing of the samples was not performed with the same Illumina and ONT method/equipment, which could have introduced specific equipment/preparation artefacts that were not considered in the study. See for example https://academic.oup.com/nargab/article/3/1/lqab019/6193612.

To our knowledge, there is no evidence that sequencing on different ONT machines or barcoding kits leads to a difference in read characteristics or accuracy. To ensure consistency and minimise potential variability, we used the same ONT flowcells for all samples and performed basecalling on the same Nvidia A100 GPU. We have updated the methods to emphasise this.

For Illumina and ONT, the exact machines and kits used for each sample have been added as supplementary table S9 We have also added a short paragraph about possible Illumina error rate differences in the ‘Limitations’ section of the Discussion.

The third limitation is that Illumina sequencing was performed on different models: three samples on the NextSeq 500 and the rest on the NextSeq 2000. While differences in error rates exist between Illumina instruments, no specific assessment has been made between these NextSeq models [42]. However, the absolute differences in error rates are minor and unlikely to impact our study significantly. This is particularly relevant since Illumina's lower F1 score compared to ONT was due to missed calls rather than erroneous ones.

In summary, while there may be specific equipment or preparation artifacts to consider, we took steps to minimise these effects and maintain consistency across our sequencing methods.

Reviewer #3 (Public Review):

Hall et al. benchmarked different variant calling methods on Nanopore reads of bacterial samples and compared the performance of Nanopore to short reads produced with Illumina sequencing. To establish a common ground for comparison, the authors first generated a variant truth set for each sample and then projected this set to the reference sequence of the sample to obtain a mutated reference. Subsequently, Hall et al. called SNPs and small indels using commonly used deep learning and conventional variant callers and compared the precision and accuracy from reads produced with simplex and duplex Nanopore sequencing to Illumina data. The authors did not investigate large structural variation, which is a major limitation of the current manuscript. It will be very interesting to see a follow-up study covering this much more challenging type of variation. 

We fully agree that investigating structural variations (SVs) would be a very interesting and important follow-up. Identifying and generating ground truth SVs is a nontrivial task and we feel it deserves its own space and study. We hope to explore this in the future.

In their comprehensive comparison of SNPs and small indels, the authors observed superior performance of deep learning over conventional variant callers when Nanopore reads were basecalled with the most accurate (but also computationally very expensive) model, even exceeding Illumina in some cases. Not surprisingly, Nanopore underperformed compared to Illumina when basecalled with the fastest (but computationally much less demanding) method with the lowest accuracy. The authors then investigated the surprisingly higher performance of Nanopore data in some cases and identified lower recall with Illumina short read data, particularly from repetitive regions and regions with high variant density, as the driver. Combining the most accurate Nanopore basecalling method with a deep learning variant caller resulted in low error rates in homopolymer regions, similar to Illumina data. This is remarkable, as homopolymer regions are (or, were) traditionally challenging for Nanopore sequencing.

Lastly, Hall et al. provided useful information on the required Nanopore read depth, which is surprisingly low, and the computational resources for variant calling with deep learning callers. With that, the authors established a new state-of-the-art for Nanopore-only variant, calling on bacterial sequencing data. Most likely these findings will be transferred to other organisms as well or at least provide a proof-of-concept that can be built upon.

As the authors mention multiple times throughout the manuscript, Nanopore can provide sequencing data in nearly real-time and in remote regions, therefore opening up a ton of new possibilities, for example for infectious disease surveillance.

However, the high-performing variant calling method as established in this study requires the computationally very expensive sup and/or duplex Nanopore basecalling, whereas the least computationally demanding method underperforms. Here, the manuscript would greatly benefit from extending the last section on computational requirements, as the authors determine the resources for the variant calling but do not cover the entire picture. This could even be misleading for less experienced researchers who want to perform bacterial sequencing at high performance but with low resources. The authors mention it in the discussion but do not make clear enough that the described computational resources are probably largely insufficient to perform the high-accuracy basecalling required. 

We have provided runtime benchmarks for basecalling in Supplementary Figure S23 and detailed these times in Supplementary Table S7. In addition, we state in the Results section (P9 L239-241) “Though we do note that if the person performing the variant calling has received the raw (pod5) ONT data, basecalling also needs to be accounted for, as depending on how much sequencing was done, this step can also be resource-intensive.”

Even with super-accuracy basecalling considered, our analysis shows that variant calling remains the most resource-intensive step for Clair3, DeepVariant, FreeBayes, Medaka, and NanoCaller. Therefore, the statement “the described computational resources are probably largely insufficient to perform the high-accuracy basecalling required”, is incorrect. However, we have made this more prominent in the Results and Discussion.

In the results section we added the underlined section:

“… FreeBayes had the largest runtime variation, with a maximum of 597s/Mbp, equating to 2.75 days for the same genome. In contrast, basecalling with a single GPU using the super-accuracy model required a median runtime of 0.77s/Mbp, or just over 5 minutes for a 4Mbp genome at 100x depth. …”

In the discussion we have added the following statement:

“Basecalling is generally faster than variant calling, assuming GPU access, which is likely considered when acquiring ONT-related equipment.”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The colour choices in Figure 3 and Figure 4 c made the illustrations somewhat difficult to read. More substantially, a deeper investigation of the causes of non-homopolymeric-related mistaken indel calls would be useful. 

We have updated Figure 3 so that each line has a different style to aid in discriminating between colours. The colour scheme for Figure 4c has also been updated.

In terms of non-homopolymeric false positive (FP) indel calls, we did an investigation of these for Clair3 and DeepVariant on the simplex sup data as these are the two best performing variant callers and deal the best with homopolymers. For Clair3, there were eight FPs across all samples. Five of these were homopolymers. The remaining three occurred within one or two bases of another insertion which inserted a similar sequence to the FP. For DeepVariant, it was much the same story, with 8/11 FP indels being in homopolymers, and the remaining three being within one or two bases of another insertion with a similar sequence. We have added a couple of sentences to the results explaining this finding.

Reviewer #2 (Recommendations For The Authors):

The paper is well-written and provides evidence for the conclusions. Some issues should be addressed.

Include a section in the Results describing species-specific observations, namely if some samples had recurrently lower SNP and INDEL F1 scores (as observed in Figure 2). 

Please see our response in your second point in the ‘Weaknesses’ section of the public review.

Please provide more details on how the samples were sequenced. Section "Sequencing" in the methods is confusing and not clear enough to be reproduced (provide a supplementary table/figure with the workflow for each sample). Add information about how many samples were multiplexed in each run and what was the output achieved in each.

We have now added a Supplementary Table S9 which outlines which instruments, kits, and multiplexing strategies were used for each sample. In addition, the raw pod5 data that we make available has been segregated by sample, so knowledge of the multiplexing strategy is not necessary for someone attempting to reproduce our results.

The authors acknowledge that structural variation was not evaluated in this manuscript. Since ONT sequencing is often used to reconstruct the sequence of plasmids for outbreak/epidemiology analysis, perhaps they could undertake this analysis on a plasmids dataset (which suffers from constant structural variation).

As noted in our response to Reviewer 3’s public review, we fully agree that investigating structural variations (SVs) would be a very interesting and important follow-up. Identifying and generating ground truth SVs is a nontrivial task and we feel it deserves its own space and study. We hope to explore this in the future.

Reviewer #3 (Recommendations For The Authors):

The manuscript is well organized. However, some sections are a bit long and would benefit from being more concise.

Thank you for your valuable feedback and for acknowledging the organisation of our manuscript. We appreciate your suggestion regarding the length of certain sections. We have gone back through and made the manuscript more concise.

Figure 1: Is the Qscore really the same as identity? Isn't the determination of identity only possible after alignment? 

When we say Qscore we are referring to the Phred-scaled version of the read identity, which is alignment based, not the Qscores of the individual bases in the FASTQ file. We have updated the text and figure legend to make this clearer. “The Qscore is the logarithmic transformation of the read identity,  , where 𝑃 is the read identity.”. We also now explicitly state that read identity is alignment-based.

Abbreviations/terms mentioned but not introduced: <br /> - kmers, P2L57

- ANI, P3L93 

We have updated the text to better introduce these terms.

eLife assessment

Notario Manzano et al. offer a valuable first analysis of proteins within tunneling nanotubes (TNTs), membranous bridges connecting cells. This work distinguishes TNTs from extracellular vesicles, but further experimental and analytical tools are needed to refine the TNT proteome. Solid data supports a role for tetraspanins CD9 and CD81 in TNT function. The proposed model for CD9 and CD81 is over-interpreted and requires additional evidence for stronger support.

eLife assessment

This valuable study demonstrates that the behavior of the cells in the presomitic mesoderm in zebrafish embryos depend on both an intrinsic program and external information, providing new insight into the biology underlying embryo axis segmentation. There is convincing support for the findings with a thorough and quantitative single-cell real-time imaging approach, both in vitro and in vivo, developed by the authors.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Rohde et al. discuss how single cells isolated from the presomitic mesoderm of the zebrafish embryo follow a cell-autonomous differentiation "programme", which is dependent on the initial anteroposterior position in the embryo.

Strengths:

This work and, in particular, the comparison to cellular behaviour in vivo presents a detailed description of the oscillatory system that brings the developmental biology forward in their understanding of somitogenesis.<br /> The main novelty lies in the direct comparison of these isolated single cells to single cells tracked within the developing embryo. This allows them to show that isolated cells follow a similar path of differentiation without direct contact to neighbours or the presence of external morphogen gradients. Based on this, the authors propose an internal timer that starts ticking as cells traverse the presomitic mesoderm, while external signals modify this behaviour.

There are a few direct questions that follow up from this study, for instance, intercellular synchronization influences the variability of the timer. However, I agree with the authors that such experiments are out of the scope of this study.

Author response:

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

Reviewer #1 (Public Review):

My main point of concern is the precision of dissection. The authors distinguish cells isolated from the tailbud and different areas in the PSM. They suggest that the cell-autonomous timer is initiated, as cells exit the tailbud.

This is also relevant for the comparison of single cells isolated from the embryo and cells within the embryo. The dissection will always be less precise and cells within the PSM4 region could contain tailbud cells (as also indicated in Figure 1A), while in the analysis of live imaging data cells can be selected more precisely based on their location. This could therefore contribute to the difference in noise between isolated single cells and cells in the embryo. This could also explain why there are "on average more peaks" in isolated cells (p. 6, l. 7).

This aspect should be considered in the interpretation of the data and mentioned at least in the discussion. (It does not contradict their finding that more anterior cells oscillate less often and differentiate earlier than more posterior ones.)

Reviewer #1 rightly points out that selecting cells in a timelapse is more precise than manual dissection. Manual dissection is inherently variable but we believe in general it is not a major source of noise in our experiments. To control for this, we compared the results of 11 manual dissections of the posterior quarter of the PSM (PSM4) with those of the pooled PSM4 data. In general, we did not see large differences in the distributions of peak number or arrest timing that would markedly increase the variability of the pooled data above that of the individual dissections (Figure 1 – supplement figure 7). We have edited the text in the Results to highlight this control experiment (page 6, lines 13-17).

It is of course possible that we picked up adjacent TB cells when dissecting PSM4, however the reviewer’s assertion that inclusion of TB cells “could also explain why there are "on average more peaks" in isolated cells” is incorrect. Later in the paper we show that cells from the TB have almost identical distributions to PSM4 (mean ± SD, PSM4 4.36 ± 1.44; TB 4.26 ± 1.35; Figure 4 _ supplement 1). Thus, inadvertent inclusion of TB cells while dissecting would in fact not increase the number of peaks.

Here, the authors focus on the question of how cells differentiate. The reverse question is not addressed at all. How do cells maintain their oscillatory state in the tailbud? One possibility is that cells need external signals to maintain that as indicated in Hubaud et al. 2014. In this regard, the definition of tailbud is also very vague. What is the role of neuromesodermal progenitors? The proposal that the timer is started when cells exit the tailbud is at this point a correlation and there is no functional proof, as long as we do not understand how cells maintain the tailbud state. These are points that should be considered in the discussion.

The reviewer asks “How do cells maintain their oscillatory state in the tailbud?”. This is a very interesting question, but as recognized by the reviewer, beyond the scope of our current paper.

We now further emphasize the point “One possibility is that cells need external signals to maintain … as indicated in Hubaud et al. 2014” in the Discussion and added a reference to the review Hubaud and Pourquié 2014 (Signalling dynamics in vertebrate segmentation. Nat Rev Mol Cell Biol 15, 709–721 (2014). https://doi.org/10.1038/nrm3891) (page 18, lines 19-22).

To clarify the definition of the TB, we have stated more clearly in the results (page 15, lines 8-12) that we defined TB cells as all cells posterior to the notochord (minus skin) and analyzed those that survived

>5 hours post-dissociation, did not divide, and showed transient Her1-YFP dynamics.

The reviewer asks: What is the role of neuromesodermal progenitors? In responding to this, we refer to Attardi et al., 2018 (Neuromesodermal progenitors are a conserved source of spinal cord with divergent growth dynamics. Development. 2018 Nov 9;145(21):dev166728. doi: 10.1242/dev.166728).

Around the stage of dissection in zebrafish in our work, there is a small remaining group of cells characterized as NMPs (Sox2 +, Tbxta+ expression) in the dorsal-posterior wall of the TB. These NMPs rarely divide and are not thought to act as a bipotential pool of progenitors for the elongating axis, as is the case in amniotes, rather contributing to the developing spinal cord. How this particular group of cells behaves in culture is unclear as we did not subdivide the TB tissue before culturing. It would be possible to specifically investigate these NMPs regarding a role in TB oscillations, but given the results of Attardi et al., 2018 (small number of cells, low bipotentiality), we argue that it would not be significant for the conclusions of the current work. To indicate this, we included a sentence and a citation of this paper in the results towards the beginning of the section on the tail bud (page 15, lines 8-12).

The authors observe that the number of oscillations in single cells ex vivo is more variable than in the embryo. This is presumably due to synchronization between neighbouring cells via Notch signalling in the embryo. Would it be possible to add low doses of Notch inhibitor to interfere with efficient synchronization, while at the same time keeping single cell oscillations high enough to be able to quantify them?

It is a formal possibility that Delta-Notch signaling may have some impact on the variability in the number of oscillations. However, we argue that the significant amount of cell tracking work required to carry out the suggested experiments would not be justified, considering what has been previously shown in the literature. If Delta-Notch signaling was a major factor controlling the variability of the intrinsic program that we describe, then we would expect that in Delta-Notch mutants the anterior- posterior limits of cyclic gene expression in the PSM would extend beyond those seen in wildtype embryos. Specifically, we might expect to see her1 expression extending more anteriorly in mutants to account for the dramatic increase in the number of cells that have 5, 6, 7 and 8 cycles in culture (Fig. 1E versus Fig. 1I). However, as shown in Holley et al., 2002 (Fig. 5A, B; her1 and the notch pathway function within the oscillator mechanism that regulates zebrafish somitogenesis. Development. 2002 Mar;129(5):1175-83. doi: 10.1242/dev.129.5.1175), the anterior limit of her1 expression in the PSM in DeltaD mutants (aei) is not different to WT. Thus, Delta-Notch signaling may exert a limited control over the number of oscillations, but likely not in excess of one cycle difference.

In the same direction, it would be interesting to test if variation is decreased, when the number of isolated cells is increased, i.e. if cells are cultured in groups of 2, 3 or 4 cells, for instance.

This is a great proposal – however the culture setup used here is a wide-field system that doesn’t allow us to accurately follow more than one cell at a time. Cells that adhere to each other tend to crawl over each other, blurring their identity in Z. This is also why we excluded dividing cells in culture from the analysis. Experiments carried out with a customized optical setup will be needed to investigate this in the future.

It seems that the initiation of Mesp2 expression is rather reproducible and less noisy (+/- 2 oscillation cycles), while the number of oscillations varies considerably (and the number of cells continuing to oscillate after Mesp2 expression is too low to account for that). How can the authors explain this apparent discrepancy?

The observed tight linkage of the Mesp onset and Her1 arrest argue for a single timing mechanism that is upstream of both gene expression events; indeed, this is one of the key implications of the paper. However, the infrequent dissociation of these events observed in FGF-treated cells suggests that more than one timing pathway could be involved, although there are other interpretations. We’ve added more discussion in the text on one vs multi-timers (page 17, lines 19-23 – page 18, line 1 - 8)., see next point.

The observation that some cells continue oscillating despite the upregulation of Mesp2 should be discussed further and potential mechanism described, such as incomplete differentiation.

This is an infrequent (5 out of 54 cells) and interesting feature of PSM4 cells in the presence of FGF. We imagine that this disassociation of clock arrest from mesp on-set timing could be the result of alterations in the thresholds in the sensing mechanisms controlling these two processes. Alternatively - as reviewer 2 argues - it might reflect multiple timing mechanisms at work. We have added a discussion of these alternative interpretations (page 17, lines 19-23 – page 18, line 1 - 8).

Fig. 3 supplement 3 B missing

It’s there in the BioRxiv downloadable PDF and full text – but seems to not be included when previewing the PDF. Thanks for the heads up.

Reviewer #2 (Public Review):

The authors demonstrate convincingly the potential of single mesodermal cells, removed from zebrafish embryos, to show cell-autonomous oscillatory signaling dynamics and differentiation. Their main conclusion is that a cell-autonomous timer operates in these cells and that additional external signals are integrated to tune cellular dynamics. Combined, this is underlying the precision required for proper embryonic segmentation, in vivo. I think this work stands out for its very thorough, quantitative, single-cell real-time imaging approach, both in vitro and also in vivo. A very significant progress and investment in method development, at the level of the imaging setup and also image analysis, was required to achieve this highly demanding task. This work provides new insight into the biology underlying embryo axis segmentation.

The work is very well presented and accessible. I think most of the conclusions are well supported. Here a my comments and suggestions:

The authors state that "We compare their cell-autonomous oscillatory and arrest dynamics to those we observe in the embryo at cellular resolution, finding remarkable agreement."

I think this statement needs to be better placed in context. In absolute terms, the period of oscillations and the timing of differentiation are actually very different in vitro, compared to in vitro. While oscillations have a period of ~30 minutes in vivo, oscillations take twice as long in vitro. Likewise, while the last oscillation is seen after 143 minutes in vivo, the timing of differentiation is very significantly prolonged, i.e.more than doubled, to 373min in vitro (Supplementary Figure 1-9). I understand what the authors mean with 'remarkable agreement', but this statement is at the risk of being misleading. I think the in vitro to in vivo differences (in absolute time scales) needs to be stated more explicitly. In fact, the drastic change in absolute timescales, while preserving the relative ones, i.e. the number of oscillations a cell is showing before onset of differentiation remains relatively invariant, is a remarkable finding that I think merits more consideration (see below).

We have changed the text in the abstract (page 1, line 28) to clarify that the agreement is in the relative slowing, intensity increases and peak numbers.

One timer vs. many timers

The authors show that the oscillation clock slowing down and the timing of differentiation, i.e. the time it takes to activate the gene mesp, are in principle dissociable processes. In physiological conditions, these are however linked. We are hence dealing with several processes, each controlled in time (and thereby space). Rather than suggesting the presence of ‘a timer’, I think the presence of multiple timing mechanisms would reflect the phenomenology better. I would hence suggest separating the questions more consistently, for instance into the following three:

a.  what underlies the slowing down of oscillations?

b.  what controls the timing of onset of differentiation?

c.  and finally, how are these processes linked?

Currently, these are discussed somewhat interchangeably, for instance here: “Other models posit that the slowing of Her oscillations arise due to an increase of time-delays in the negative feedback loop of the core clock circuit (Yabe, Uriu, and Takada 2023; Ay et al. 2014), suggesting that factors influencing the duration of pre-mRNA splicing, translation, or nuclear transport may be relevant. Whatever the identity, our results indicate the timer ought to exert control over differentiation independent of the clock.”(page 14). In the first part, the slowing down of oscillations is discussed and then the authors conclude on 'the timer', which however is the one timing differentiation, not the slowing down. I think this could be somewhat misleading.

To help distinguish the clock’s slowing & arrest from differentiation, we have clarified the text in how we describe our experiments using her1-/-; her7-/- cells (page 10, lines 9-20).

From this and previous studies, we learn/know that without clock oscillations, the onset of differentiation still occurs. For instance in clock mutant embryos (mouse, zebrafish), mesp onset is still occurring, albeit slightly delayed and not in a periodic but smooth progression. This timing of differentiation can occur without a clock and it is this timer the authors refer to "Whatever the identity, our results indicate the timer ought to exert control over differentiation independent of the clock." (page 14). This 'timer' is related to what has been previously termed 'the wavefront' in the classic Clock and Wavefront model from 1976, i.e. a "timing gradient' and smooth progression of cellular change. The experimental evidence showing it is cell-autonomous by the time it has been laid down,, using single cell measurements, is an important finding, and I would suggest to connect it more clearly to the concept of a wavefront, as per model from 1976.

We have been explicit about the connection to the clock & wavefront in the discussion (page 17, line 12-17).

Regarding question a., clearly, the timer for the slowing down of oscillations is operating in single cells, an important finding of this study. It is remarkable to note in this context that while the overall, absolute timescale of slowing down is entirely changed by going from in vivo to in vitro, the relative slowing down of oscillations, per cycle, is very much comparable, both in vivo and in vivo.

We have now pointed out the relative nature of this phenomenon in the abstract, page 1, line 28.

To me, while this study does not address the nature of this timer directly, the findings imply that the cell-autonomous timer that controls slowing down is, in fact, linked to the oscillations themselves. We have previously discussed such a timer, i.e. a 'self-referential oscillator' mechanism (in mouse embryos, see Lauschke et al., 2013) and it seems the new exciting findings shown here in zebrafish provide important additional evidence in this direction. I would suggest commenting on this potential conceptual link, especially for those readers interested to see general patterns.

While we posit that the timer provides positional info to the clock to slow oscillations and instruct its arrest – we do not believe that “the findings imply that the cell-autonomous timer that controls slowing down is, in fact, linked to [i.e., governed by] the oscillations themselves.”. As we show, in her1-/-; her7-/- embryos lacking oscillations, the timing / positional information across the PSM still exists as read-out by Mesp expression. Is this different positional information than that used by the clock? – possibly – but given the tight linkage between Mesp onset and the timing/positioning of clock arrest, both cell-autonomously and in the embryo, we argue that the simplest explanation is that the timing/positional information used by the clock and differentiation are the same. Please see page 10, lines 9-20, as well as the discussion (page 17, lines 19-23; page 18. Lines 1-8 ).

We agree that the timer must communicate to the clock– but this does not mean it is dependent on the clock for positional information.

Regarding question c., i.e. how the two timing mechanisms are functionally linked, I think concluding that "Whatever the identity, our results indicate the timer ought to exert control over differentiation independent of the clock." (page 14), might be a bit of an oversimplification. It is correct that the timer of differentiation is operating without a clock, however, physiologically, the link to the clock (and hence the dependence of the timescale of clock slowing down), is also evident. As the author states, without clock input, the precision of when and where differentiation occurs is impacted. I would hence emphasize the need to answer question c., more clearly, not to give the impression that the timing of differentiation does not integrate the clock, which above statement could be interpreted to say.

As far as we can tell, we do not state that “without clock input, the precision of when and where differentiation occurs is impacted”, and we certainly do not want to give this impression. In contrast, as mentioned above, the her1-/-; her7-/- mutant embryo studies indicate that the lack of a clock signal does not change the differentiation timing, i.e. it does not integrate the clock. Of course, in the formation of a real somite in the embryo, the clock’s input might be expected to cause a given cell to differentiate a little earlier or later so as to be coordinated with its neighbors, for example, along a boundary. But this magnitude of timing difference is within one clock cycle at most, and does not match the large variation seen in the cultured cells that spans over many clock cycles.

A very interesting finding presented here is that in some rare examples, the arrest of oscillations and onset of differentiation (i.e. mesp) can become dissociated. Again, this shows we deal here with interacting, but independent modules. Just as a comment, there is an interesting medaka mutant, called doppelkorn (Elmasri et al. 2004), which shows a reminiscent phenotype "the Medaka dpk mutant shows an expansion of the her7 expression domain, with apparently normal mesp expression levels in the anterior PSM.". The authors might want to refer to this potential in vivo analogue to their single cell phenotype.

Thank you, we had forgotten this result. Although we do not agree that this result necessarily means there are two interacting modules, we have included a citation to the paper, along with a discussion of alternative explanations for the dissociation (page 18, lines 2-14).

One strength of the presented in vitro system is that it enables precise control and experimental perturbations. A very informative set of experiments would be to test the dependence of the cell-autonomous timing mechanisms (plural) seen in isolated cells on ongoing signalling cues, for instance via Fgf and Wnt signaling. The inhibition of these pathways with well-characterised inhibitors, in single cells, would provide important additional insight into the nature of the timing mechanisms, their dependence on signaling and potentially even into how these timers are functionally interdependent.

We agree and in future experiments we are taking advantage of this in vitro system to directly investigate the effect of signaling cues on the intrinsic timing mechanism.

eLife assessment

This study provides valuable information about the microbiome and metabolome, and their correlation with acute myocardial infarction. However, the relationship established between these variables is limited to a correlation, and therefore the strength of the evidence is incomplete.

Reviewer #1 (Public Review):

Summary:

The authors aimed to identify potential biomarkers for acute myocardial infarction (AMI) through blood metabolomics and fecal microbiome analysis. They found that long chain fatty acids (LCFAs) could serve as biomarkers for AMI and demonstrated a correlation between LCFAs and the gut microbiome. Additionally, in silico molecular docking and in vitro thrombogenic assays showed that these LCFAs can induce platelet aggregation.

Strengths:

The study utilized a comprehensive approach combining blood metabolomics and fecal microbiome analysis.

The findings suggest a novel use of LCFAs as biomarkers for AMI.

The correlation between LCFAs and the gut microbiome is a significant contribution to understanding the interplay between gut health and heart disease.

The use of in silico and in vitro assays provides mechanistic insights into how LCFAs may influence platelet aggregation.

Weaknesses:

The evidence is incomplete as it does not definitively prove that gut dysbiosis contributes to fatty acid dysmetabolism.

The study primarily shows an association between the gut microbiome and fatty acid metabolism without establishing causation.

Reviewer #2 (Public Review):

Summary:

Fan et al. investigated the relationship between early acute myocardial infarction (eAMI) and disturbances in the gut microbiome using metabolomics and metagenomics analyses. They studied 30 eAMI patients and 26 healthy controls, finding elevated levels of long-chain fatty acids (LCFA) in the plasma of eAMI patients.

Strengths:

The research attributed a substantial portion of LCFA variance in eAMI to changes in the gut microbiome, as indicated by omics analyses. Computational profiling of gut bacteria suggested structural variations linked to LCFA variance. The authors also conducted molecular docking simulations and platelet assays, revealing that eAMI-associated LCFAs may enhance platelet aggregation.

Weaknesses:

The results should be validated using different assays, and animal models should be considered to explore the mechanisms of action.

Author Response:

Reviewer #1 (Public Review):

Summary:

The authors aimed to identify potential biomarkers for acute myocardial infarction (AMI) through blood metabolomics and fecal microbiome analysis. They found that long chain fatty acids (LCFAs) could serve as biomarkers for AMI and demonstrated a correlation between LCFAs and the gut microbiome. Additionally, in silico molecular docking and in vitro thrombogenic assays showed that these LCFAs can induce platelet aggregation.

Strengths:

The study utilized a comprehensive approach combining blood metabolomics and fecal microbiome analysis.

The findings suggest a novel use of LCFAs as biomarkers for AMI.

The correlation between LCFAs and the gut microbiome is a significant contribution to understanding the interplay between gut health and heart disease.

The use of in silico and in vitro assays provides mechanistic insights into how LCFAs may influence platelet aggregation.

Weaknesses:

The evidence is incomplete as it does not definitively prove that gut dysbiosis contributes to fatty acid dysmetabolism.

We appreciate this reviewer’s insightful comment regarding the causal relationship between gut dysbiosis and fatty acid dysmetabolism. We acknowledge that our study primarily demonstrates a strong association rather than causation. While establishing causality was beyond the scope of the current study, we recognize the importance of addressing this point. In our revised manuscript, we will emphasize the observational nature of our findings and discuss the need for future research, including longitudinal studies and interventional trials, to explore the causal links between gut dysbiosis and fatty acid dysmetabolism. We believe that this clarification strengthens the interpretation of our results and aligns with the reviewer's concern.

The study primarily shows an association between the gut microbiome and fatty acid metabolism without establishing causation.

We agree with the reviewer that our study presents an association rather than definitive proof of causation between the gut microbiome and fatty acid metabolism. To address this, we plan to expand the discussion section to more clearly outline the limitations of our study in establishing causality. We will also propose future research directions, such as the use of animal models and longitudinal human studies, which could help elucidate the causal pathways. By clarifying this aspect, we aim to provide a more balanced perspective on our findings.

Reviewer #2 (Public Review):

Summary:

Fan et al. investigated the relationship between early acute myocardial infarction (eAMI) and disturbances in the gut microbiome using metabolomics and metagenomics analyses. They studied 30 eAMI patients and 26 healthy controls, finding elevated levels of long-chain fatty acids (LCFA) in the plasma of eAMI patients.

Strengths:

The research attributed a substantial portion of LCFA variance in eAMI to changes in the gut microbiome, as indicated by omics analyses. Computational profiling of gut bacteria suggested structural variations linked to LCFA variance. The authors also conducted molecular docking simulations and platelet assays, revealing that eAMI-associated LCFAs may enhance platelet aggregation.

Weaknesses:

The results should be validated using different assays, and animal models should be considered to explore the mechanisms of action.

We appreciate the reviewer’s suggestion to validate our findings using additional assays and animal models. We agree that further validation is crucial to confirm the robustness of our results and to explore the underlying mechanisms in greater detail. While our current study focused on human subjects and in vitro assays to establish initial findings, we acknowledge that additional experimental approaches are necessary. In the revised manuscript, we plan to include a discussion on the potential use of different assays (e.g., advanced metabolomics techniques, multi-omics integration) and animal models to validate and expand upon our findings. Moreover, we are planning to undertake these experiments in future studies to build upon the foundational work presented here.

We believe that our revised responses and the planned manuscript revisions will address the reviewers’ concerns effectively. We are confident that these changes will enhance the overall contribution of our study to the field. Thank you again for your valuable feedback.

eLife assessment

This important study advances our understanding of the mechanisms of neuronal large dense-core vesicle (LDCV) secretion, which mediates neuropeptide and neurotrophin release. It describes a negative regulatory process involving the interaction of the Rab3-effector Rabphilin-3A with the SNARE fusion protein SNAP25, which limits LDCV secretion and neurite growth. The evidence in support of the authors' claims is generally convincing, but some conclusions, e.g regarding the role of Rabphilin-3A-controlled neurotrophin signaling in neurite growth, are incompletely supported. This study will be of interest to the fields of cell biology, cellular neuroscience, and neuroendocrinology.

Joint Public Review

The molecular mechanisms that mediate the regulated exocytosis of neuropeptides and neurotrophins from neurons via large dense-core vesicles (LDCVs) are still incompletely understood. Motivated by their earlier discovery that the Rab3-RIM1 pathway is essential for neuronal LDCV exocytosis, the authors now examined the role of the Rab3 effector Rabphilin-3A in neuronal LDCV secretion. Based on live, confocal, and super-resolution imaging approaches, the authors provide evidence for a synaptic enrichment of Rabphilin-3A and for independent trafficking of Rabphilin-3A and LDCVs. Using an elegant NPY-pHluorin imaging approach, they show that genetic deletion of Rabphilin-3A causes an increase in electrically triggered LDCV fusion events and increased neurite length. Finally, knock-out-replacement studies, involving Rabphilin-3A mutants deficient in either Rab3- or SNAP25-binding, indicate that the synaptic enrichment of Rabphilin-3A depends on its Rab3 binding ability, while its ability to bind to SNAP25 is required for its effects on LDCV secretion and neurite development. The authors conclude that Rabphilin-3A negatively regulates LDCV exocytosis and propose that this mechanism also affects neurite growth, e.g. by limiting neurotrophin secretion. These are important findings that advance our mechanistic understanding of neuronal large dense-core vesicle (LDCV) secretion.

The major strengths of the present paper:

(i) The use of a powerful Rabphilin-3A KO mouse model.<br /> (ii) Stringent lentiviral expression and rescue approaches as a strong genetic foundation of the study.<br /> (iii) An elegant FRAP imaging approach.<br /> (iv) A cutting-edge NPY-pHluorin-based imaging approach to detect LDCV fusion events.

Weaknesses of the present paper:

(i) It remains unclear why a process that affects a general synaptic SNARE fusion protein - SNAP25 - would specifically affect LDCV but not synaptic vesicle fusion.<br /> (iii) The mechanistic links between Rabphilin-3A function, LDCV density in neurites, neurite outgrowth, and the proposed underlying mechanisms involving trophic factor release remain unresolved.

Author response:

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

Public Reviews:

Joint Public Review: 

The molecular mechanisms that mediate the regulated exocytosis of neuropeptides and neurotrophins from neurons via large dense-core vesicles (LDCVs) are still incompletely understood. Motivated by their earlier discovery that the Rab3-RIM1 pathway is essential for neuronal LDCV exocytosis, the authors now examined the role of the Rab3 effector Rabphilin-3A in neuronal LDCV secretion. Based on multiple live and confocal imaging approaches, the authors provide evidence for a synaptic enrichment of Rabphilin-3A and for independent trafficking of Rabphilin-3A and LDCVs. Using an elegant NPY-pHluorin imaging approach, they show that genetic deletion of Rabphilin-3A causes an increase in electrically triggered LDCV fusion events and increased neurite length. Finally, knock-out-replacement studies, involving Rabphilin-3A mutants deficient in either Rab3- or SNAP25-binding, indicate that the synaptic enrichment of Rabphilin-3A depends on its Rab3 binding ability, while its ability to bind to SNAP25 is required for its effects on LDCV secretion and neurite development. The authors conclude that Rabphilin-3A negatively regulates LDCV exocytosis and propose that this mechanism also affects neurite growth, e.g. by limiting neurotrophin secretion. These are important findings that advance our mechanistic understanding of neuronal large dense-core vesicle (LDCV) secretion. 

The major strengths of the present paper are: 

(i) The use of a powerful Rabphilin-3A KO mouse model. 

(ii) Stringent lentiviral expression and rescue approaches as a strong genetic foundation of the study. 

(iii) An elegant FRAP imaging approach. 

(iv) A cutting-edge NPY-pHluorin-based imaging approach to detect LDCV fusion events. 

We thank the reviewers for their positive evaluation of our manuscript.

Weaknesses that somewhat limit the convincingness of the evidence provided and the corresponding conclusions include the following: 

(i) The limited resolution of the various imaging approaches introduces ambiguity to several parameters (e.g. LDCV counts, definition of synaptic localization, Rabphilin-3A-LDCV colocalization, subcellular and subsynaptic localization of expressed proteins, AZ proximity of Rabphilin-3A and LDCVs) and thereby limits the reliability of corresponding conclusions. Super-resolution approaches may be required here. 

We thank the reviewer for their constructive suggestion. We fully agree that super-resolution imaging would produce a more precise localization of RPH3A and co-localization with DCVs. We have now repeated our (co)-localization experiments with STED microscopy. We find that RPH3A colocalized with the pre-synaptic marker Synapsin1 and, to a lesser extent, with the post synaptic marker Homer and DCV marker chromogranin B (new Figure 1). This indicates that RPH3A is highly enriched in synapses, mostly the pre-synapse, and that RPH3A partly co-localizes with DCVs.  

(ii) The description of the experimental approaches lacks detail in several places, thus complicating a stringent assessment. 

We apologize for the lack of detail in explaining the experimental approaches. We have included a more detailed description in the revised manuscript. 

(iii) Further analyses of the LDCV secretion data (e.g. latency, release time course) would be important in order to help pinpoint the secretory step affected by Rabphilin-3A. 

We agree. To address this comment, we have now included the duration of the fusion events (new Figure S2D-F). The start time of the fusion events are shown in the cumulative plots in now Figure 3F and I. The kinetics are normal in the RPH3A KO neurons.

(iv) It remains unclear why a process that affects a general synaptic SNARE fusion protein - SNAP25 - would specifically affect LDCV but not synaptic vesicle fusion. 

We agree that we have not addressed this issue systematically enough in the original manuscript. We have now added a short discussion on this topic in the Discussion of the revised manuscript (p 15, line 380-386). In brief, we do not claim full selectivity for the DCV pathway. Some effects of RPH3A deficiency on the synaptic vesicle cycle have been observed. Furthermore, because DCVs typically do not mix in the synaptic vesicle cluster and fuse outside the active zone (and outside the synapse), DCVs might be more accessible to RPH3A regulation.

(v) The mechanistic links between Rabphilin-3A function, LDCV density in neurites, neurite outgrowth, and the proposed underlying mechanisms involving trophic factor release remain unclear. 

We agree that we have not addressed all these links systematically enough in the original manuscript, although we feel that we have at least postulated the best possible working model to link RPH3A function to DCV exocytosis/neurotrophic factor release and neurite outgrowth (p 15-16, line 396-400). Of course, a single study cannot support all these links with sufficient experimental evidence. We have now added a short text on what we can conclude exactly based on our experiments and how we see the links between RPH3A function, DCV exocytosis/neurotrophic factor release, neurite outgrowth and DCV density in neurites (p 13-14, line 317-325).

Reviewer #1 (Public Review): 

Summary:

The manuscript by Hoogstraaten et al. investigates the effect of constitutive Rabphilin 3A (RPH3A) ko on the exocytosis of dense core vesicles (DCV) in cultured mouse hippocampal neurons. Using mCherry- or pHluorin-tagged NPY expression and EGFP- or mCherry tagged RPHA3, the authors first analyse the colocalization of DCVs and RPH3A. Using FRAP, the authors next analyse the mobility of DCVs and RAB3A in neurites. The authors go on to determine the number of exocytotic events of DCVs in response to high-frequency electrical stimulation and find that RPH3A ko increases the number of exocytotic events by a factor 2-3, but not the fraction of released DCVs in a given cell (8x 50Hz stim). In contrast, the release fraction is also increased in RBP3A KOs when doubling the stimulation number (16x 50Hz). They further observe that RPH3A ko increases dendrite and axon length and the overall number of ChgrB-positive DCVs. However, the overall number of DCVs and dendritic length in ko cells directly correlate, indicating that the number of vesicles per dendritic length remains unaffected in the RPH3A KOs. Lentiviral co-expression of tetanus toxin (TeNT) showed a non-significant trend to reduce axon and dendrite length in RPH3a KOs. Finally, the authors use co-expression of RAB3A and SNAP25 constructs to show that RAB3A but not SNAP25 interaction is required to allow the exocytosis-enhancing effect in RPH3A KOs. 

While the authors' methodology is sound, the microscopy results are performed well and analyzed appropriately, but their results in larger parts do not sufficiently support their conclusions. Moreover, the experiments are not always described in sufficient detail (e.g. FRAP; DCV counts vs. neurite length) to fully understand their claims. 

Overall, I thus feel that the manuscript does not provide a sufficient advance in knowledge. 

Strengths: 

- The authors' methodology is sound, and the microscopy results are performed well and analyzed appropriately. 

- Figure 2: The exocytosis imaging is elegant and potentially very insightful. The effect in the RPH3A KOs is convincing. 

- Figure 4: the logic of this experiment is elegant. It shows that the increased number of DCV fusion events in RPH3A KOs is related to the interaction of RPH3A with RAB3A but not with SNAP25. 

We thank the reviewer for their positive evaluation of our manuscript.

Weaknesses: 

- The results in larger parts do not sufficiently support the conclusions. 

- The experiments are not always described in sufficient detail (e.g. FRAP; DCV counts vs. neurite length) to fully understand their claims. 

- Not of sufficient advance in knowledge for this journal 

- The significance of differences in control experiments WT vs. KO) varies between experiments shown in different figures. 

- Axons and dendrites were not analyzed separately in Figures 1 and 2. 

- The colocalization study in Figure 1 would require super-resolution microscopy. 

To address the reviewers’ comments, we have provided a more detailed explanation of our analysis (p 19-20, line 521-542). In addition, we have repeated our colocalization experiments using STED microscopy, see Joint Public Review item (i).  

Reviewer #2 (Public Review): 

Summary: 

Hoogstraaten et al investigated the involvement of rabphilin-3A RPH3A in DCV fusion in neurons during calcium-triggered exocytosis at the synapse and during neurite elongation. They suggest that RPH3A acts as an inhibitory factor for LDV fusion and this is mediated partially via its interaction with SNAP25 and not Rab3A/Rab27. It is a very elegant study although several questions remain to be clarified. 

Strengths: 

The authors use state-of-the-art techniques like tracking NPY-PHluorin exocytosis and FRAP experiments to quantify these processes providing novel insight into LDCs exocytosis and the involvement of RPH3A. 

We thank the reviewer for their positive evaluation of our manuscript.

Weaknesses: 

At the current state of the manuscript, further supportive experiments are necessary to fully support the authors' conclusions. 

We thank the reviewer for their comments and suggestions. We have performed additional experiments to support our conclusions, see Joint Public Review items (i) – (iv)

Reviewer #3 (Public Review): 

Summary: 

The molecular mechanism of regulated exocytosis has been extensively studied in the context of synaptic transmission. However, in addition to neurotransmitters, neurons also secrete neuropeptides and neurotrophins, which are stored in dense core vesicles (DCVs). These factors play a crucial role in cell survival, growth, and shaping the excitability of neurons. The mechanism of release for DCVs is similar, but not identical, to that used for SV exocytosis. This results in slow kinetic and low release probabilities for DCV compared to SV exocytosis. There is a limited understanding of the molecular mechanisms that underlie these differences. By investigating the role of rabphilin-3A (RPH3A), Hoogstraaten et al. uncovered for the first time a protein that inhibits DCV exocytosis in neurons. 

Strengths: 

In the current work, Hoogstraaten et al. investigate the function of rabphilin-3A (RPH3A) in DVC exocytosis. This RAB3 effector protein has been shown to possess a Ca2+ binding site and an independent SNAP25 binding site. Using colocalization analysis of confocal imaging the authors show that in hippocampal neurons RPH3A is enriched at pre- and post-synaptic sites and associates specifically with immobile DCVs. Using site-specific RPH3A mutants they found that the synaptic location was due to its RAB3 interaction site. They further could show that RPH3A inhibits DCV exocytosis due to its interaction with SNAP25. They came to that conclusion by comparing NPY-pHluorin release in WT and RPH3A KO cells and by performing rescue experiments with RPH3A mutants. Finally, the authors showed that by inhibiting stimulated DCV release, RPH3A controlled the axon and dendrite length possibly through the reduced release of neurotrophins. Thereby, they pinpoint how the proper regulation of DCV exocytosis affects neuron physiology. 

We thank the reviewer for their positive evaluation of our manuscript.

Weaknesses: 

Data context 

One of the findings is that RPH3A accumulates at synapses and is mainly associated with immobile DCVs.

However, Farina et al. (2015) showed that 66% of all DCVs are secreted at synapses and that these DCVs are immobile prior to secretion. To provide additional context to the data, it would be valuable to determine if RPH3A KO specifically enhances secretion at synapses. Additionally, the authors propose that RPH3A decreases DCV exocytosis by sequestering SNAP25 availability. At first glance, this hypothesis appears suitable. However, due to RPH3A synaptic localization, it should also limit SV exocytosis, which it does not. In this context, the only explanation for RPH3A's specific inhibition of DCV exocytosis is that RPH3A is located at a synapse site remote from the active zone, thus protecting the pool of SNAP25 involved in SV exocytosis from binding to RPH3A. This hypothesis could be tested using super-resolution microscopy. 

We thank the reviewer for their suggestion. We have now performed super resolution microscopy, see Joint Public Review item (i). However, these new data do not necessarily explain the stronger effect of RP3A deficiency on DCV exocytosis, relative to SV exocytosis. We have added a short discussion on this topic to the revised manuscript, see Joint Public Review item (iv).

Technical weakness 

One technical weakness of this work consists in the proper counting of labeled DCVs. This is significant since most findings in this manuscript rely on this analysis. Since the data was acquired with epi-fluorescence or confocal microscopy, it doesn't provide the resolution to visualize individual DCVs when they are clumped. The authors use a proxy to count the number of DCVs by measuring the total fluorescence of individual large spots and dividing it by the fluorescence intensity of discrete spots assuming that these correspond to individual DCVs. This is an appropriate method but it heavily depends on the assumption that all DCVs are loaded with the same amount of NPY-pHluorin or chromogranin B (ChgB). Due to the importance of this analysis for this manuscript, I suggest that the authors show that the number of DCVs per µm2 is indeed affected by RPH3A KO using super-resolution techniques such as dSTORM, STED, SIM, or SRRF. 

The reviewer is correct that this is a crucial issue, that we have not addressed optimally until now. We have previously devoted a large part of a previous manuscript to this issue, but have not referred to this previous work clearly enough. We have now clarified this (p 7, line 187-190). In brief, we have previously quantified the ratio between fluorescent intensity of ChgB and NPY-pHluorin in confocal microscopy over the number of dSTORM puncta in sparse areas of WT mouse hippocampal neurons (Persoon et al., 2018). This quantification yielded a unitary fluorescence intensity per vesicle that was very stable of different neurons. Although there might be some underestimation of the total number of DCVs when using confocal microscopy, the study of Persoon et al. (2018) has demonstrated that these parameters correlate well and that the estimations are accurate. Considering that the rF/F0 is similar in RPH3A WT and KO neurons (now Figure S2I), meaning that the intensity of NPY-pHluorin of one fusion event is comparable, we can presume that this correlation also applies for the RPH3A KO neurons.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Major points: 

(1) The authors perform an extensive analysis regarding the colocalization of RPH3A and DCVs (Figure 1 upper part). This analysis is hampered by the fact that the recorded data has in relation to vesicle size limited resolution (> 1 µm) to allow making strong claims here. In my view, super-resolution microscopy would be required for the co-localization studies shown in Figure 1. 

We fully agree and have now performed super-resolution microscopy, see Joint Public Review item (i)

(2) The FRAP experiments (Figure 1 lower part) cannot be sufficiently understood from what is presented. The methods say that both laser channels were activated during bleaching but NPY-pHluorin is not bleached in Fig.1E. Explanation of the bleaching is not very circumspect. In 1D, it is rather EGFP-RPH3A that is entering the bleached area than the NPY vesicles. These experiments require a more careful explanation of methodology, observed results, and their interpretation. Overall, the observed effects in the original kymograph traces require a better explanation. 

We acknowledge that NPY-pHluorin in Figure 1E (now Figure 2C) is not completely bleached. NPY-pHluorin appeared to be more difficult to bleach than NPY-mCherry. However, it is important to clarify that we merely bleached the neurites to remove the stationary puncta and facilitate our analysis of DCV/RPH3A dynamics. This bleaching step does not affect the interpretation of our results. We apologize that this was not clearly stated in the text and have made the necessary adjustments in legend, results- and methods section, (p 6-7, line 162-163; p 5, line 140-142 and p 19, line 508-513). Additionally, we apologize for the accidental switch of the kymographs for NPY-mCherry and EGFP-RPH3A in Figure 1D (now Figure 2B, C). We greatly appreciate identifying this error.  

(3) Figure 1: The authors need to mention whether axons, dendrites, or both were analyzed throughout the different panels and how they were identified. Is it possible that axons were wrapping around dendrites in their cultures (compare e.g. Shimojo et al., 2015)? Given the limited spatial resolution and because of this wrapping, interpretation of results could be affected. 

We completely agree with the reviewer’s assessment and conclusion. We are unable to distinguish axons from dendrites using this experimental design. We have made sure to specify in the text that our observation that RPH3A does not co-travel with DCVs is true for both dendrites and axons, (p 5, line 150).

(4) Figure 2: The exocytosis imaging is elegant and potentially very insightful. The effect in the RPH3A KOs is convincing. However, the authors determine the efficacy of exocytosis from NPY-pHluorin unquenching of DCVs only. This is only one of several possible parameters to read out the efficiency of exocytosis. Kinetics like e.g. delay between stimulation and start of exocytosis events or release time course of NPY after DCV fusion were not determined. Such analysis could give a better insight into what process before or after the fusion of DCVs is affected by RPH3A ko. 

We fully agree with the reviewer. We have now included the duration of the fusion events (new Figure S2D-F). The start time of the fusion events are shown in the cumulative plots in now Figure 3F and I. The kinetics are normal in the RPH3A KO neurons.

Moreover, it needs to be mentioned whether 2C and D are from WT or ko cultures. It would be best to show representative examples from both genotypes. 

We have now adjusted this in the new figure (now Figure 3C, D).

The number of fusion events is much increased but the release fraction is not significantly changed. While this is consistent with results in Figure 4C it is at variance with 4F. This raises questions about the reliability of the effects in RPH3A KOs. 

The release fraction indicates the number of fusion events normalized to the total DCV pool. In Figure 4D, we observed a slightly bigger pool size, which explains the lack of significance when analyzing the released fraction. In Figure 4G, however, DCV pool sizes are similar between KO and WT, leading to a statistically significant effect on release fraction in KO neurons. Furthermore, Figures 4B and E distinctly show a substantial increase in fusion events in RPH3A KO neurons. This variability in pool size observed could potentially be attributed to variation in culture or inherent biological variability.

Given the increased number of ChgrB-positive DCVs in RPH3A KOs (shown in Figure 2) and that only the cumulative number of exocytosis events were analysed, how can the authors exclude that the RPH3A ko only affects vesicle number but not release, if the % change in released vesicles is not different to WT? Kinetics of release don't seem to be affected. Importantly, what was the density of NPY-pHluorin vesicles in WT vs. ko? 

In Figure 2 (now Figure 5) we show that RPH3A KO neurons are larger and contain more endogenous ChgB+ puncta than WT neurons. This increased number of ChgrB+ puncta scales with their size as puncta density is not increased. A previous study (Persoon et al., 2018) has demonstrated a strong correlation between DCV number and neuron size. Our data show that RPH3A deficiency increased DCV exocytosis, but the released fraction of vesicles depends on the total number of DCVs, which we determined during live recording by dequenching NPY-pHluorin using NH4+. Considering that this is an overexpression of a heterologous DCV-fusion reporter, and not endogenous staining of DCVs, as in the case of ChgrB+ puncta, some variability is not unexpected.

Also in these experiments, the question arises of whether the authors analyse axons, dendrites, or both throughout the different panels and how they were identified. 

In our experimental design we record all fusion events per cell, including both axons and dendrites but excluding the cell soma. We have clarified this in the method section, (p 19, line 508 and p 19, line 521-522).

(5) Figure 3: in D the authors show that ChgrB-pos. DCV density is slightly increased in KOs. How does this relate to the density of NPY-pHluorin DCVS in Figure 2? 

We do not observe a difference in NPY-pHluorin density (see Author response image 1). However, it is important to note that we relied on tracing neurites in live recording images to determine the neuronal size. In contrast, the ChgB density was based on dendritic length using MAP2 (post-hoc) staining was limited. In addition, Chgr+ puncta represent an endogenous DCV staining, NPY-pHluorin quantification is based on overexpression of a heterologous DCV-fusion reporter. These two factors likely contribute some variability.

Author response image 1.

The authors show a non-significant trend of TeNT coexpression to reduce axon and dendrite lengths in RPH3A KOs. While this trend is visible, I think one cannot draw conclusions from that when not reaching significance. The argument of the authors that the increased axon and dendrite lengths are created by growth factor peptide release from DCV during culture time is interesting. However, the fact that TeNT expression shows a trend toward reducing this effect on axons/dendrites is not sufficient to prove the release of such growth factors. 

We agree. We have toned down this speculation in the revised manuscript, (p 15-16, line 395-400).

Lastly, the authors don't provide insight into the mechanisms, of how RPH3A ko increases the number of DCVs per µm dendritic length in the neurons. In my view, there are too many loose ends in this story of how RPH3A ko first increases spontaneous release of DCVs and then enhances neurite growth and DCV density. Did the authors e.g. measure the spontaneous release of DCVs in their cultures? 

We measured spontaneous release of DCVs during the 30s baseline recording prior to stimulation. We observed no difference in spontaneous release between WT and KO neurons (now Figure S2H). However, baseline recording lasted only 30 seconds. It is possible that this was too short to detect subtle effects.

Other points: 

(1) Figure 4: the logic of this experiment is elegant. It shows that the increased number of DCV fusion events in RPH3A KOs is related to the interaction of RPH3A with RAB3A but not with SNAP25. As mentioned above, it is irritating that the reduction of fusion events in KOs and on the release fraction is sometimes reaching significance, but sometimes it does not. Likewise, the absence of significant effects on DCV numbers is not consistent with the results shown in Figures 3C and D. 

DCV numbers in Figure 3 (now Figure 5) are determined by staining for endogenous ChgB, whereas in Figure 4D and G DCV numbers are determined by overexpressing NPY-pHluorin and counting the dequenched puncta following a NH4+ puff.

(2) Figure 1B: truncation of the y-axis needs to be clearly indicated. 

We have replaced this figure with new Figure 1 and have indicated truncations of the y-axis when needed (new Figure 1E). 

(3) Page 10: "Given that neuropeptides are key modulators of adult neurogenesis (Mu et al., 2010), and that RPH3A depletion leads to increased DCV exocytosis, it is coherent that we observed longer neurites in RPH3A KO neurons." I cannot follow the argument of the authors here: what has neurogenesis to do with neurite length? 

We apologize for the confusion. We have clarified this in the revised text, (p 16, line 398-400).

Minor point: 

There are some typos in the manuscript. e.g., page 8: "... may partially dependent on regulated secretion...); page 6: "...to dequence all...". 

Thank you for noticing, we have corrected the typos.

Reviewer #2 (Recommendations For The Authors): 

(1) Supplementary Figure S1A, in my opinion, should be in Figure 1A as it illustrates all the constructs used in this study and helps the reader to follow it up. 

We thank the reviewer for their suggestion. However, we feel that with the adjustments we have made in Figure 1, the illustrations of the constructs fit better in Figure S1, since new Figure 1 shows the localization of endogenous RPH3A and not that of the constructs.  

(2) One of the conclusions of the manuscript is the synaptic localization of the different RPH3A mutants. The threshold for defining synaptic localization is not clear either from the images nor from the analysis: for example, the Menders coefficient for VGut1-Syn1 which is used as a positive control, ranges from 0.65-0.95 and that of RPH3A and Syn1 ranges from 0.5-0.95. These values should be compared to all mutants and the conclusions should be based on such comparison. 

We agree. We have now repeated our initial co-localization experiment with all the RPH3A mutants (now Figure S1D-F).  

(3) Strengthening this figure with STED/SIM/dSTORM microscopy can verify and add a new understanding of the subtle changes of RPH3A localization. 

We fully agree and have now added super-resolution microscopy data, see Joint Public Review item (i).

(4) As RAB3A/RAB27A (ΔRAB3A/RAB27A) loses the punctate distribution, please clarify how can it function at the synapse and not act as a KO. Is it sorted to the synapse and how does it is sorted to the synapse? 

We used lentiviral delivery to introduce our constructs, resulting in the overexpression of ΔRAB3A/RAB27A mutant RPH3A. This overexpression likely compensates for the loss of the punctate distribution of RPH3A, thereby maintaining its limiting effect on DCV exocytosis. It is plausible that under physiological conditions, the mislocalization of RPH3A would lead to increased exocytosis, similar to what we observed in the KO. 

(5) Is RPH3A expressed in both excitatory and inhibitory neurons? 

We agree this is an important question. Single cell RNA-seq already suggests the protein is expressed in both, but we nevertheless decided to test expression of RPH3A protein in excitatory and inhibitory neurons, using immunocytochemistry with VGAT and VGLUT as markers in hippocampal and striatal WT neurons. We found that RPH3A is expressed in both VGLUT+ hippocampal neurons and VGAT+ striatal neurons (new Figure S1A, B).  

(6) The differential use of ChgB and NPY as markers for DCVs should be clarified and compared as these are used at different stages of the manuscript. 

We have previously addressed the comparison between ChgB and NPY-pHluorin (Persoon et al., 2018). We made sure to indicate this more clearly throughout the manuscript to clarify the use of the two markers. 

(7) FRAP experiments- A graph describing NPY recovery should be added as a reference to 2H and discussed. 

We agree. We have made the necessary adjustments (new Figure 2G).

(8) Figure 2E shows some degree of "facilitation" between the 2 8x50 pulses RPH3A KO neurons. Can the author comment on that? What was the reason for using this dual stimulation protocol? 

There is indeed some facilitation between the two 8 x 50 pulses in KO neurons and to a lesser extent also in the WT neurons, which we have observed before in WT neurons (Baginska et al., 2023). Baginska et al. (2023) showed recently that different stimulation protocols can influence certain fusion dynamics, like the ratio of persistent and transient events and event duration. We used two different stimulation protocols to thoroughly investigate the effect of RPH3A on exocytosis, and assess the robustness of our findings regarding the number of fusion events. Fusion kinetics was similar in WT an KO neurons for both stimulation protocols (new Figure 2D-F).

(9) Figure 3 quantifies dendrites length and then moves to quantify both axon and dendrites for the Tetanus toxin experiment. What are the effects of KO on axon length? In the main figures, it is not mentioned but in S3 it seems not to be affected. How does it reconcile with the main conclusion on neurite length? 

Figure 3H (now Figure 6C) shows the effect of the KO on axon length: the axon length is increased in RPH3A KO neurons compared to WT, similar to dendrite length. Re-expressing RPH3A in KO neurons rescues axonal length to WT levels. In Figure S3, we observe a similar trend as in main Figure 3 (new Figure 6), yet this effect did not reach significance. Based on this, we concluded that neurite length is increased upon RPH3A depletion.

(10) For lay readers, please explain the total pool and how you measured it. However, see the next comment. 

We agree. We have now defined this better in the revised manuscript, (p 19, line 524-527 and p 20, line 535-539).

(11) It is a bit hard to understand if the total number of DCV was increased in the KO and if the pool size was increased and in which figure it is quantified. Some sentences like: "A trend towards a larger intracellular DCV pool in KO compared to WT neurons was observed" do not fit with "No difference in DCV pool size was observed between WT and KO neurons (Figure S2D)" or with "During stronger stimulation (16 bursts of 50 APs at 50 Hz), the total fusion and released fraction of DCVs were increased in KO neurons compared to WT". They are not directly supported, or not related to specific figures. Please indicate if the total DCVs pool, as measured by NH4, was increased and based on that, the fraction of the releasable DCVs following the long stimulation. From Figure 2H, the conclusion is an increase in fusion events. In general, NH4 is not quantified clearly- is it quantified in Figure S2C? And if it is a trend, how can it become significant in Figure 3? 

We agree there has been some inconsistency in the way we describe the data on the total number of DCVs. We have addressed this in the revised text to ensure better clarity. The total DCV pool measured by NPY-pHluorin was not significantly increased in KO neurons, we see a trend towards a bigger DCV pool in the 2x8 50 Hz stimulation paradigm (now Figure S2C), therefore the released fraction of vesicles is not increased in Figure 1G (now Figure 3G). The number of DCV in Figure 3 (now Figure 5) is based on endogenous ChgB staining and not overexpression like the DCV pool measured by NPY-pHluorin. In Figure 3 (now Figure 5) we show that RPH3A KO neurons have slightly more ChgB+ puncta compared to WT.

(12) In Figure 3, the quantification is not clear, discrete puncta are not visible but rather a smear of chromogranin staining. How was it quantified? An independent method to count DCV number, size, and distribution like EM is necessary to support and add further understanding. 

We acknowledge that discrete ChgB puncta are not completely visible in Figure 3 (now Figure 5). Besides the inherent limitation in resolution with confocal imaging, we believe that this is due to ChgB accumulation in the KO neurons, as shown in now Figure 5D. Nonetheless, to address this concern of the reviewer, we have selected other images that represent our dataset (now Figure 5A). Furthermore, the number of ChgB+ DCVs was calculated using SynD software (Schmitz et al., 2011; van de Bospoort et al., 2012) (see previous reply). EM would offer valuable independent confirmation on the total DCV number, size and distribution. However, with the current method we already know that vesicle numbers are at least similar. Does that justify the (major) investment in a quantitative EM study? Moreover, this issue does not affect the central message of the current study.

(13) Can the author discuss if the source of DCVs that are released at the synapse is similar or different from the source of DCVs fused while neurites elongate? 

With our current experimental design, we are unable to draw conclusions regarding this aspect. We are not sure how experiments to identify this source (probably the Golgi?) would be crucial to sustain the central message of our study.

(14) An interesting and related question: what are the expression levels of RPH3A during development and neuronal growth during the nervous system development? 

While we have not specifically examined the expression levels of RPH3A over development, public databases show that RPH3A expression increases over time in mice, consistent with other synaptic proteins (Blake et al., 2021; Baldarelli et al., 2021; Krupke et al., 2017). We have now added this to the revised manuscript (p 2, line 55-56).

(15) The conclusion from Figure 4 about the contribution of SNAP25 interaction to RPH3A inhibitory effect is not convincing. The data are scattered and in many neurons, high levels of fusion events were detected. Further or independent experiments are needed to support this conclusion. For example, is the interaction with SNAP25 important for its inhibitory activity in other DCV-releasing systems like adrenal medulla chromaffin cells? 

We agree that further studies in other DCV-releasing systems like chromaffin cells would provide valuable insight into the role of SNAP25 interaction in RPH3A’s inhibitory effect on exocytosis. However, we believe that starting new series of experiments in another model system is outside of the scope of our current study.

(16) Furthermore, the number of DCVs in the KO is similar in this experiment, raising some more questions about the quantification of the number of vesicles, that differ, in different sections of the manuscript (points # 10,11). 

The total DCV pool in the fusion experiments is measured by overexpression NPY-pHluorin, this cannot be directly compared to the number of endogenous ChgB+ DCV in Figure 3 (now Figure 5), see also item (11)

(17) The statement - "RPH3A is the only negative regulator of DCV" is not completely accurate as other DCV inhibitors like tomosyn were described before. 

We agree. By this statement, we intend to convey that RPH3A is the only negative regulator of DCVs without substantial impact on synaptic vesicle exocytosis, unlike Tomosyns. We have clarified this in the revised text, (p 15, line 366-367).

(18) The support for the effect of KO on the "clustering of DCVs" is not convincing. 

The intensity of endogenous ChgB puncta was decreased in RPH3A KO neurons (now Figure 5E). However, the peak intensity induced by single NPY-pHluorin labeled DCV fusion events (quanta) was unchanged (now Figure S2I). This indicates that the decrease in ChgB puncta intensity must be due to a reduced number of DCVs (quanta) in this specific location. We have interpreted that as ‘clustering’, or maybe ‘accumulation’. However, we only put forward this possibility. We are now more careful in our speculations within the text, (p 11 line 271-277).

(19) Final sentence: "where RPH3A binds available SNAP25, consequently restricting the assembly of SNARE complexes" should be either demonstrated or rephrased as no effect of trans or general SNARE complex formation is shown. 

We agree. We have made the necessary adjustments in the text, (p 15, line 387-389).   

(20) A scheme summarizing RPH3A's interaction with synaptic proteins and its effects on DCVs release, maybe even versus its effects on SVs release, should be considered as a figure or graphic abstract. 

We have included a working model in Figure 7.  

(21) Figure 4 logically should come after Figure 2 to summarize the fusion-related chapter before moving to neurite elongation. 

We have placed Figure 4 after Figure 2 (now Figure 3).

Reviewer #3 (Recommendations For The Authors): 

One important finding of this study is that RPH3A downregulates neuron size, possibly by inhibiting DCV release. Additionally, the authors demonstrated that the number of DCVs is directly proportional to the number of DCVs per µm2, and that RPH3A KO reduces DCV clustering. This conclusion was drawn by comparing ChgB with NPY-pHluorin loading of the DCVs. However, this comparison is not valid as ChgB is expressed at an endogenous level and NPY-pHluorin is over-expressed. In the KO situation where DCV exocytosis is enhanced, the available endogenous ChgB may be depleted faster than the overexpressed NPY-pHluorin. Hoogstraaten et al. should either perform a study in which ChgB is overexpressed to test whether the difference in DCV remains or at least provides an alternative interpretation of their data. 

We thank the reviewer for this comment. The reviewer challenges one or two conclusions in our original manuscript (It is not entirely clear to what exactly “This conclusion” refers): (a) “the number of DCVs is directly proportional to the number of DCVs per µm2”, and (b) “that RPH3A KO reduces DCV clustering”. The reviewer probably means that the number of DCVs per neuron is directly proportional to size of the neuron (a) and states this (these) conclusion(s) are “not valid as ChgB is expressed at an endogenous level and NPY-pHluorin is over-expressed” because “endogenous ChgB may be depleted faster than the overexpressed NPY-pHluorin”. We have three arguments to conclude that faster depletion of ChgB cannot affect these two conclusions: (1) DCVs bud off from the Golgi with newly synthesized (fresh) ChgB. Whether or not a larger fraction of DCVs is released does not influence this initial ChgB loading into DCVs (together with over-expressed NPY-pHluorin); (2) in hippocampal neurons merely 1-6% of the total DCV pool undergoes exocytosis (the current study and also extensively demonstrated in Persoon et al., 2018). RPH3A KO neurons release few percent more of the total DCV pool. Hence, “depletion of ChgB” is only marginally different between experimental groups; and (c) the proposed experiment overexpressing ChgB will not help scrutinize our current conclusions as ChgB overexpression is known to affect DCV biogenesis and the total DCV pool, most likely much more than a few percent more release by RPH3A deficiency.

Hoogstraaten et al. conducted a thorough analysis of the impact of RPH3A KO and its rescue using various mutants on dendrite and axon length (see Supplementary Figure 3). However, they did not test the effect of the ΔSNAP25 mutant. The authors demonstrated that this mutant is the least efficient in rescuing DCV exocytosis (Figure 4E). Hence the neurons expressing this mutant should have a similar size to the KO neurons. This finding would strongly support the argument that DCV exocytosis regulates neuron size. Otherwise, it would suggest that RPH3A may have a function in regulating exocytosis at the growth cones that is independent of SNAP25. Since the authors most probably have the data that allows them to measure the neuron size (acquired for Supplementary Figure 2), I suggest that they perform the required analysis. 

We agree this is important and performed new experiments to determine the dendrite length of RPH3A WT, KO and KO neurons expressing the ΔSNAP25 mutant. We observed that the dendrite length of RPH3A KO neurons expressing ΔSNAP25 mutant is indeed similar to KO neurons (new Figure S3C). Although not significant we observe a clear trend towards bigger neurons compared to WT.  This strengthens our conclusion that increased DCV exocytosis contributes to the observed increased neuronal size.

The authors displayed the result of DCV exocytosis in two ways. One is by showing the number of exocytosis events the other is to display the proportion of DCVs that were secreted. They do the latter by dividing the secreted DCV by the total number of DCVs. These are visualized at the end of the experiment through NH4+ application. While this method works well for synaptic secretion as the marker of SV is localized to the SV membrane and remains at the synapse upon SV exocytosis, it cannot be applied in the same manner when it is the DCV content that is labeled as it is released upon secretion. Hence, the total pool of vesicles should be the number of DCV counted upon NH4+ application in addition to those that are secreted. This way of analyzing the total pool of DCV might also explain the difference in this pool size between KO neurons stimulated two times with 8 stimuli instead of one time with 16 stimuli (Sup Fig 2 C and D). This is an important point as it affects the conclusions drawn from Figure 2. 

We thank the reviewed for this comment. We agree, and we have made the necessary adjustments throughout the manuscript. 

The kymogram of DCV exocytic events displayed in Figure 2D shows a majority of persistent (>20s long) events. This is strange as NPY-pHluori corresponds to the released cargo. Previous work using the same labeling and stimulation technique showed that content release occurs in less than 10s (Baginska et al. 2023). The authors should comment on that difference. 

In Baginska et al. (2023), the authors distinguished between persistent and transient events. The transient events are shorter than 10s for the 2x8 and 16x stimulation paradigms, whereas persistent events can last for more than 10s. In our study we did not make this distinction. However, in response to this reviewer, we have now quantified the fusion duration per cell. These new data show that the mean duration is similar between genotypes for both stimulation paradigms. We have added these new data (new Figure S2D-F).

In Figures 1D and E, some puncta in the kymogram appeared to persist after bleaching. This raises questions about the effectiveness of the bleaching procedure for the FRAP experiment. 

The reviewer is correct that NPY-pHluorin in Figure 1E (now Figure 2C) is not fully bleached. NPY-pHluorin was more resistant to bleaching than NPY-mCherry. However, we merely bleached the neurites to facilitate our analysis by reducing fluorescence of the stationary puncta without causing phototoxicity. Some remaining fluorescence after bleaching does not affect our conclusions in any way.

In the discussion, the paragraph titled "RPH3A does not travel with DCVs in hippocampal neurons" is quite confusing and would benefit from a streamlined explanation. 

We thank the reviewed for this comment. We made the necessary adjustments to make this paragraph clearer, (p 14, line 339-351).

First paragraph of page 8 "TeNT expression in KO neurons restored neurite length to WT levels. When compared to KO neurons without TeNT, neurite length was not significantly decreased but displayed a trend towards WT levels (Figure 3G, H)." These two sentences are confusing as they seem contradictory. 

We agree that this conclusion has been too strong. However, we do not see a contradiction. The significant effect between KO and control neurons on both axon and dendrite length is lost upon TeNT expression (which forms the basis for our conclusions cited by the reviewer, now Figure 6B, C). While the difference between KO neurons +/- TeNT did not reach statistical significance. The (strong) trend is clearly in the same direction. We have refined our original conclusion in the revised manuscript, (p 12, line 304-306).

The data availability statement is missing. 

We have added the data availability statement, (p 21, line 571-572).

eLife assessment

This is an important paper on the role of engrams and relevant conditions that influence memory and forgetting. The variety of methods used, namely, behavioural, labeling, interrogation, immunohistochemistry, microscopy, pharmacology, computational, are exemplary and provide convincing evidence for the role of engrams in the dentate gyrus in memory retrieval and forgetting. This examination will be of interest broadly across behavioural and neural science communities.

Reviewer #1 (Public Review):

O'Leary and colleagues sought to understand the factors that underlie memory processes, including formation, retrieval, and forgetting. The present data identify time, environmental enrichment, Rac-1, context reexposure, and brief reminders of the familiar object as factors that alter discrimination between novel and familiar objects. This is complimented with an engram approach to quantify cells that are active during learning to examine how their activation is impacted with each of the above factors at test. There are many strengths in the manuscript, including systematic testing of several factors that contribute to poor discrimination between novel and familiar objects. These results are interesting and outline essential boundaries of incidental, nonaversive memory. With this behavioral data, authors apply a modeling approach to understand the factors that contribute to good and poor object memory recall.

Reviewer #2 (Public Review):

Summary:

The manuscript examines an important question about how an inaccessible, natural forgotten memory can be retrieved through engram ensemble reactivation. It uses a variety of strategies including optogenetics, behavioral and pharmacological interventions to modulate engram accessibility. The data characterize the time course of natural forgetting using an object recognition task, in which animals can retrieve 1 day and 1 week after learning, but not 2 weeks later. Forgetting is correlated with lower levels of cell reactivation (c-fos expression during learning compared to retrieval) and reduction in spine density and volume in the engram cells. Artificial activation of the original engram was sufficient to induce recall of the forgotten object memory while artificial inhibition of the engram cells precluded memory retrieval. Mice housed in an enriched environment had a slower rate of forgetting, and a brief reminder before the retrieval session promoted retrieval of a forgotten memory. Repeated reintroduction to the training context in the absence of objects accelerated forgetting. Additionally, activation of Rac1-mediated plasticity mechanisms enhanced forgetting, while its inhibition prolonged memory retrieval. Authors also reproduce the behavioral findings using a computational model inspired by Rescorla-Wagner model. In essence, the model proposes that forgetting is a form of adaptive learning that can be updated based on prediction error rules in which engram relevancy is altered in response to environmental feedback.

Strengths:

(1) The data presented in the current paper are consistent with the authors claim that seemingly forgotten engrams are, in fact, accessible. This suggests that retrieval deficits can lead to memory impairments rather than a loss of the original engram (at least in some cases).

(2) The experimental procedures and statistics are appropriate, and the behavioral effects appear to be very robust. Several key effects are replicated multiple times in the manuscript.

Comments on revised version:

The authors have adequately addressed my prior concerns.

Reviewer #3 (Public Review):

Summary:

The manuscript by Ryan and colleagues uses a well-established object recognition task to examine memory retrieval and forgetting. They show that memory retrieval requires activation of the acquisition engram in the dentate gyrus and failure to do so leads to forgetting. Using a variety of clever behavioural methods, the authors show that memories can be maintained and retrieval slowed when animals are reared in environmental enrichment and that normally retrieved memories can be forgotten if exposed to the environment in which the expected objects are no longer presented. Using a series of neural methods, the authors also show that activation or inhibition of the acquisition engram is key to memory expression and that forgetting is due to Rac1.

Strengths:

This is an exemplary examination of different conditions that affect successful retrieval vs forgetting of object memory. Furthermore, the computational modelling that captures in a formal way how certain parameters may influence memory provides an important and testable approach to understanding forgetting.<br /> The use of the Rescorla-Wanger model in the context of object recognition and the idea of relevance being captured in negative prediction error are novel (but see below).<br /> The use of gain and loss of function approaches are a considerable strength and the dissociable effects on behaviour eliminate the possibility of extraneous variables such as light artifacts as potential explanations for the effects.

Weaknesses:

A closer examination of the process that governs the behavioural effect in the present investigation would have been of even greater significance. The authors acknowledge the distinction between object familiarity vs object recognition, but a direct assessment would benefit the field's understanding of the current role of engrams on behaviour.

Relatedly, while relevance is an interesting concept that has been operationalized in the paper, it is unclear how distinct it is from extinction. Specifically, in the case where the animals are exposed to the context in the absence of the object, the paper currently expresses this as a process of relevance - the objects are no longer relevant in that context. Another way to think about this is in terms of extinction - the association between the context and the objects is reduced resulting in a disrupted ability of the context to activate the object engram. The authors have noted the potential role of extinction in their studies.

The impact of the paper is somewhat limited by the use of only one sex. Do the authors expect an identical process to be engaged in females in the present set of studies?

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

O'Leary and colleagues present data identifying several procedures that alter discrimination between novel and familiar objects, including time, environmental enrichment, Rac-1, context reexposure, and brief reminders of the familiar object. This is complimented with an engram approach to quantify cells that are active during learning to examine how their activation is impacted following each of the above procedures at test. With this behavioral data, authors apply a modeling approach to understand the factors that contribute to good and poor object memory recall.

We thank the Reviewer for summarizing the scope and depth of our manuscript, and indeed for recognizing our efforts. We engage below with the Reviewer’s specific criticisms.

Strengths:

Authors systematically test several factors that contribute to poor discrimination between novel and familiar objects. These results are extremely interesting and outline essential boundaries of incidental, nonaversive memory.<br /> These results are further supported by engram-focused approaches to examine engram cells that are reactivated in states with poor and good object recognition recall.

We thank the Reviewer for these positive comments.

Weaknesses:

For the environmental enrichment, authors seem to suggest objects in the homecage are similar to (or reminiscent of) the familiar object. Thus, the effect of improved memory may not be related to enrichment per se as much as it may be related to the preservation of an object's memory through multiple retrievals, not the enriching experiences of the environment itself. This would be consistent with the brief retrieval figure. Authors should include a more thorough discussion of this.

This is one of the main issues highlighted by the Editor and the Reviewers. We agree that these results dove-tail with the reminder experiments. We have included additional discussion, see line 510-546.

Authors should justify the marginally increased number of engram cells in the non-enrichment group that did not show object discrimination at test, especially relative to other figures. More specific cell counting criteria may be helpful for this. For example, was the DG region counted for engram and cfos cells or only a subsection?

There was a marginal, but non-significant increase in the number of labelled cells within the standard housed mice in Figure 3f. The cell counting criteria was the same across experimental groups and conditions, where the entire dorsal and ventral blade of the dorsal DG was counted for each animal. This non-statistically significant variance may be due to surgical and viral spread difference between mice. We have clarified this in the manuscript, see line 229-232.

It is unclear why the authors chose a reactivation time point of 1hr prior to testing. While this may be outside of the effective time window for pharmacological interference with reconsolidation for most compounds, it is not necessarily outside of the structural and functional neuronal changes accompanied by reconsolidation-related manipulations.

A control experiment was performed to demonstrated that a brief reminder exposure of 5 mins on its own was insufficient to induce new learning that formed a lasting memory (Supplementary Figure S4a). Mice given only a brief acquisition period of 5 mins, exhibited no preference for the novel object when tested 1 hour after training, suggesting the absence of a lasting object memory (Supplementary Figure S4b & c). We therefore used the 1-hour time point for the brief reminder experiment in Figure 4a. We have clarified this within the manuscript and supplementary data see line 258-264.

Figure 5: Levels of exploration at test are inconsistent between manipulations. This is problematic, as context-only reexposures seem to increase exploration for objects overall in a manner that I'm unsure resembles 'forgetting'. Instead, cross-group comparisons would likely reveal increased exploration time for familiar and novel objects. While I understand 'forgetting' may be accompanied by greater exploration towards objects, this is inconsistent across and within the same figure. Further, this effect is within the period of time that rodents should show intact recognition. Instead, context-only exposures may form a competing (empty context) memory for the familiar object in that particular context.

The Reviewer raises an important question, and we agree with the Reviewer that there should be caution and qualification around interpreting these results as “forgetting”. Indeed, for the context-only rexposures, cross-group comparisons show increased exploration time for familiar and novel objects. As the mice exhibit relatively high exploration of both the novel and familiar objects. An alternative explanation would be that the mice have not truly forgotten the familiar object, but rather as the mouse has not seen the familiar object in the last 6 context only sessions, its reappearance makes it somewhat novel again. Therefore, this change in the object’s reappearance triggers the animal’s curiosity, and in turn drives exploration by the animal. In addition, the context-only exposures may form a competing memory for the familiar object in that particular context. We have highlighted this in the results and also included greater discussion. See lines 306-315.

I am concerned at the interpretation that a memory is 'forgotten' across figures, especially considering the brief reminder experiments. Typically, if a reminder session can trigger the original memory or there is rapid reacquisition, then this implies there is some savings for the original content of the memory. For instance, multiple context retrievals in the absence of an object reminder may be more consistent with procedures that create a distinct memory and subsequently recruit a distinct engram.

These findings raise an important question regarding the interpretation of ‘forgetting’. If a reminder trial or experience can trigger the original memory, or there is rapid reacquisition, then this would suggest there is a degree of savings for the original memory content (85, 86). Previous work has emphasized retrieval deficits as a key characteristic of memory impairment, supporting the idea that memory recall or accessibility may be driven by learning feedback from the environment (7, 8, 14–18). Within our behavioral paradigm, a lack of memory expression would still constitute forgetting due to the loss of learned behavioral response in the presence of natural retrieval cues. The changes in memory expression may therefore underlie the adaptive nature of forgetting. This is consistent with the idea that the engram is intact and available, but not accessible. Here we studied natural forgetting, and our data showing memory retrieval following optogenetic reactivation demonstrates that the original engram persists at a cellular level, otherwise activation of those cells would no longer trigger memory recall. We also agree with the reviewer that multiple context retrievals may indeed lead to the formation of a second distinct engram that competes with the original. Recent work suggests that retroactive interference emerges from the interplay of multiple engrams competing for accessibility (18). We have added clarification and included extra discission of this interpretation. See lines 589-598.

Authors state that spine density decreases over time. While that may be generally true, there is no evidence that mature mushroom spines are altered or that this is consistent across figures. Additionally, it's unclear if spine volume is consistently reduced in reactivated and non-reactivated engram cells across groups. This would provide evidence that there is a functionally distinct aspect of engram cells that is altered consistently in procedures resulting in poor recognition memory (e.g. increased spine density relative to spine density of non-reactivated engram cells and non-engram cells)

We thank the Reviewer for their helpful comments on explaining our engram dendritic spine data. We agree with the Reviewer that an analysis of the changes in spine type, as well as the difference between engram and non-engram spines as well and reactivation and non-reactivated engram spines would be interesting and may help to further illuminate the morphological changes of forgetting and memory retrieval. Indeed, future analysis could determine if spine density is reduced in reactivated and non-reactivated engram cells or indeed across engram non-engram cells within different learning conditions. This avenue of investigation could determine if there is a functionally distinct aspect of engram cells that are altered following forgetting (67). However, such analysis is beyond the scope of this study. We have highlighted this limitation and included its discussion. See lines 493-499.

Authors should discuss how the enrichment-neurogenesis results here are compatible with other neurogenesis work that supports forgetting.

We validated the effectiveness of the enrichment paradigm to enhance neural plasticity by measuring adult hippocampal neurogenesis. The hippocampus has been identified as one of the only regions where postnatal neurogenesis continues throughout life (75). Levels of adult hippocampal neurogenesis do not remain constant throughout life and can be altered by experience (41–43, 57).  In addition, adult born neurons have been shown to contribute to the process of forgetting (74, 78, 79). Although the contribution of adult born neurons to cognition and the memory engram is not fully understood (80, 81). Mishra et al, showed that immature neurons were actively recruited into the engram following a hippocampal-dependent task (67). Moreover, increasing the level of neurogenesis rescued memory deficits by restoring engram activity (67). Augmenting neurogenesis further rescued the deficits in spine density in both immature and mature engram neurons in a mouse model of Alzheimer’s disease (67). Whether neurogenesis alters spine density on differentially for reactivated or non-reactivation engrams cells remains to be investigated (67, 68). This avenue of research would help to illuminate the morphological changes following forgetting and provide evidence if there is a functionally distinct aspect of engram cells that is altered in forgetting (67, 68). Our engram labelling strategy which utilized c-fos-tTA transgenic mice combined with an AAV9-TRE-ChR2-eYFP virus does not necessarily label sufficient immature neurons. Future work could utilize a different engram preparation, such as a genetic labelling strategy (TRAP2) or using a different immediate early gene promoter such as Arc to investigate the contribution of new-born neurons to the engram ensemble. We have added additional discussion of how our work fits with previous literature investigating neurogenesis and forgetting. See lines 547-565.

Reviewer #2 (Public Review):

Summary:

The manuscript examines an important question about how an inaccessible, natural forgotten memory can be retrieved through engram ensemble reactivation. It uses a variety of strategies including optogenetics, behavioral and pharmacological interventions to modulate engram accessibility. The data characterize the time course of natural forgetting using an object recognition task, in which animals can retrieve 1 day and 1 week after learning, but not 2 weeks later. Forgetting is correlated with lower levels of cell reactivation (c-fos expression during learning compared to retrieval) and reduction in spine density and volume in the engram cells. Artificial activation of the original engram was sufficient to induce recall of the forgotten object memory while artificial inhibition of the engram cells precluded memory retrieval. Mice housed in an enriched environment had a slower rate of forgetting, and a brief reminder before the retrieval session promoted retrieval of a forgotten memory. Repeated reintroduction to the training context in the absence of objects accelerated forgetting. Additionally, activation of Rac1-mediated plasticity mechanisms enhanced forgetting, while its inhibition prolonged memory retrieval. The authors also reproduce the behavioral findings using a computational model inspired by Rescorla-Wagner model. In essence, the model proposes that forgetting is a form of adaptive learning that can be updated based on prediction error rules in which engram relevancy is altered in response to environmental feedback.

We thank the Reviewer for summarizing the scope and depth of our manuscript, and for recognizing our efforts. We engage below the Reviewer’s specific criticisms of our interpretations.

Strengths:

(1) The data presented in the current paper are consistent with the authors claim that seemingly forgotten engrams sometimes remain accessible. This suggests that retrieval deficits can lead to memory impairments rather than a loss of the original engram (at least in some cases).

We thank the Reviewer for their positive summary.

(2) The experimental procedures and statistics are appropriate, and the behavioral effects appear to be very robust. Several key effects are replicated multiple times in the manuscript.

We thank the Reviewer for their positive comments.

Weaknesses:

(1) My major issue with the paper is the forgetting model proposed in Figure 7. Prior work has shown that neutral stimuli become associated in a manner similar to conditioned and unconditioned stimuli. As a result, the Rescorla-Wagner model can be used to describe this learning (Todd & Homes, 2022). In the current experiments, the neutral context will become associated with the unpredicted objects during training (due to a positive prediction error). Consequently, the context will activate a memory for the objects during the test, which should facilitate performance. Conversely, any manipulation that degrades the association between the context and object should disrupt performance. An example of this can be found in Figure 5A. Exposing the mice to the context in the absence of the objects should violate their expectations and create a negative prediction error. According to the Rescorla-Wagner model, this error will create an inhibitory association between the context and the objects, which should make it harder for the former to activate a memory of the latter (Rescorla & Wagner, 1972). As a result, performance should be impaired, and this is what the authors find. However, if the cells encoding the context and objects were inhibited during the context-alone sessions (Figure 5D) then no prediction error should occur, and inhibitory associations would not be formed. As a result, performance should be intact, which is what the authors observe.

What about forgetting of the objects that occurs over time? Bouton and others have demonstrated that retrieval failure is often due to contextual changes that occur with the passage of time (Bouton, 1993; Rosas & Bouton, 1997, Bouton, Nelson & Rosas, 1999). That is, both internal (e.g. state of the animal) and external (e.g. testing room, chambers, experimenter) contextual cues change over time. This shift makes it difficult for the context to activate memories with which it was once associated (in the current paper, objects). To overcome this deficit, one can simply re-expose animals to the original context, which facilitates memory retrieval (Bouton, 1993). In Figure 2D, the authors do something similar. They activate the engram cells encoding the original context and objects, which enhances retrieval.

Therefore, the forgetting effects presented in the current paper can be explained by changes in the context and the associations it has formed with the objects (excitatory or inhibitory). The results are perfectly predicted by the Rescorla-Wagner model and the context-change findings of Bouton and others. As a result, the authors do not need to propose the existence of a new "forgetting" variable that is driven by negative prediction errors. This does not add anything novel to the paper as it is not necessary to explain the data (Figures 7 and 8).

We thank the reviewer for clearly explaining their concern about our model. We are very sorry that we did not sufficiently explain that our model is, in fact, based on the classic Rescorla-Wagner model. The key equation of the model that updates “engram strength”  is equivalent to the canonical Rescorla-Wagner model that is commonly used in research on reinforcement learning and decision-making (105). One potential minor difference is that we crucially assume different learning rates for positive and negative prediction errors. However, this variant of the Rescorla-Wagner model is common in the computational literature and is generally not regarded as a qualitatively different kind of model. In fact, it allows us to capture that establishing an object-context association (after a positive prediction error) is faster than the forgetting process (through negative errors).

The other equations that are explained in detail in the Methods are necessary to simulate exploration behavior and render the model suitable for model fitting. Concerning exploration behavior, we use the softmax function, which is commonly used in combination with the Rescorla-Wager model, in order to translate the learned quantity (in our case, engram strength) into behavior (here exploration). The other equations are necessary to fit the model to the data (learning rate α and behavioral variability in exploration behavior).

Therefore, we fully agree with the reviewer that the Rescorla-Wagner can explain our empirical results, in particular by assuming that the different manipulations affect the strength of object-context associations, which, in turn, governs forgetting as behaviorally observed. 

In our previous version of the manuscript, we only referred to the Rescorla-Wagner model directly in the Methods. But to make this important point clearer, we now refer to the origin of the model multiple times in the Results section as well. See lines 81, 386-393.

We also agree with the reviewer that the learning/forgetting process can be described in terms of changes in object-context associations (e.g., inhibitory associations after a negative prediction error). Therefore, we now explicitly refer to the relationship between updated object-context associations and forgetting and highlight that we believe that stronger associations signal higher engram “relevancy”. See lines 386-393.

We have extended Figure 7 (new panels a and b), where we illustrate the idea that (a) object-context associations govern forgetting and (b) show the key Rescorla-Wagner equation, including a simple explanation of the main terms (engram strength, prediction error, and learning rate). Finally, we have also extended our discussion of the model, where we now directly state that the Rescorla-Wagner model captures the key results of our experiments. See lines 573-580.

In order to further support a link between our empirical data and computational modeling, we also added extra experiments that showed the modulation of engram cells within the dentate gyrus can regulate these object-context associations. See Supplementary Figure 12a-f and lines 401-404.

To summarize our reply, we agree with the reviewer’s comment and hope that we have clarified the direct relationship to the Rescorla-Wagner model.

(2) I also have an issue with the conclusions drawn from the enriched environment experiment (Figure 3). The authors hypothesize that this manipulation alleviates forgetting because "Experiencing extra toys and objects during environmental enrichment that are reminiscent of the previously learned familiar object might help maintain or nudge mice to infer a higher engram relevancy that is more robust against forgetting.". This statement is completely speculative. A much simpler explanation (based on the existing literature) is that enrichment enhances synaptic plasticity, spine growth, etc., which in turn reduces forgetting. If the authors want to make their claim, then they need to test it experimentally. For example, the enriched environment could be filled with objects that are similar or dissimilar to those used in the memory experiments. If their hypothesis is correct, only the similar condition should prevent forgetting.

We thank the Reviewer for this alternative perspective on our findings. First of all, we agree that this statement is speculative. The effects of enrichment on neural plasticity are well established and it likely contributes to the enhanced memory recall. It is important to emphasize that this process of updating is not necessarily separate from enrichment-induced plasticity at an implementational level, but part of the learning experience within an environment containing multiple objects. The enrichment or, more generally, experience, may therefore enhance memory through the modification of activity of specific engram ensembles. The idea of enrichment facilitating memory updating is consistent with the results obtained by the reminder experiments and further supported by our analysis with the Rescorla-Wagner computational model, where experience updates the accessibility of existing memories, possibly through reactivation of the original engram ensemble.

We would like to further clarify that our explanation concerns the algorithmic level, in contrast to the neural level. Based on the computational analyses using the Rescorla-Wagner model and in line with the reviewer’s previous comment on the model, we believe that forgetting is governed by the strength of object-context associations (or engram relevancy). Our interpretation is that stronger associations signal that the memory or engram representation is important ("relevant") and should not be forgotten. Accordingly, due to a vast majority of experiences with extra cage objects in the enriched environment, mice might generally learn that such objects are common in their environment and potentially relevant in the future (i.e., the object-context association is strong, preventing forgetting). Our speculation of these results is to help unify our empirical data with the computational model.

We believe that the Reviewer's alternative explanation in terms of synaptic plasticity, spine growth is not mutually exclusive with the modelling work. It is possible that the computational mechanisms that we explore based on the Rescorla-Wagner model are neuronally related to the biological mechanisms that the reviewer suggests at the implementational level. Therefore, ultimately, the two perspectives might even complement each other. We have included additional discussion to clarify this point. See lines 510-546.

(3) It is well-known that updating can both weaken or strengthen memory. The authors suggest that memory is updated when animals are exposed to the context in the absence of the objects. If the engram is artificially inhibited (opto) during context-only re-exposures, memory cannot be updated. To further support this updating idea, it would be good to run experiments that investigate whether multiple short re-exposures to the training context (in the presence of the objects or during optogenetic activation of the engram) could prevent forgetting. It would also be good to know the levels of neuronal reactivation during multiple re-exposures to the context in the absence versus context in the presence of the objects.

We thank the Reviewer for their comments. We agree that additional experiments would be helpful to further support the idea of updating. We have performed additional experiments to test the idea that multiple short re-exposures to the training context, in the presence of objects prevents forgetting. In this paradigm, mice were repeatedly exposed to the original object pair (Supplementary Figure S5a). The results indicate that repeated reminder trials facilitate object memory recall (Supplementary Figure 5b&c). These data indicated that subsequent object reminders over time facilitates the transition of a forgotten memory to an accessible memory. See Supplementary Figure S5 and Lines 279-287.

(4) There are a number of studies that show boundary conditions for memory destabilization/reconsolidation. Is there any evidence that similar boundary conditions exist to make an inaccessible engram accessible?

The Reviewer asks an interesting question about boundary conditions and engram accessibility. Boundary conditions could indeed affect the degree of destabilization and reconsolidation, the salience or strength of the memory, as well as the timing of retrieval cues. Future models could focus on understanding the specific boundary conditions in which a memory becomes retrievable and the degree to which it is sufficiently destabilized and liable for updating and forgetting. We have included additional discussion on the potential role of boundary conditions for engram accessibility. See lines 661-666.

(5) More details about how the quantification of immunohistochemistry (c-fos, BrdU, DAPI) was performed should be provided (which software and parameters were used to consider a fos positive neurons, for example).

We have added additional information for the parameters of quantification of immunohistochemistry. See lines 796-809.

(6) Duration of the enrichment environment was not detailed.

We have highlighted the details for the environmental enrichment duration. See lines 756.

Reviewer #3 (Public Review):

Summary:

The manuscript by Ryan and colleagues uses a well-established object recognition task to examine memory retrieval and forgetting. They show that memory retrieval requires activation of the acquisition engram in the dentate gyrus and failure to do so leads to forgetting. Using a variety of clever behavioural methods, the authors show that memories can be maintained and retrieval slowed when animals are reared in environmental enrichment and that normally retrieved memories can be forgotten if exposed to the environment in which the expected objects are no longer presented. Using a series of neural methods, the authors also show that activation or inhibition of the acquisition engram is key to memory expression and that forgetting is due to Rac1.

We thank the Reviewer for summarizing the scope and depth of our manuscript, and indeed for recognizing our efforts. We engage below the Reviewer’s specific criticisms of our interpretations.

Strengths:

This is an exemplary examination of different conditions that affect successful retrieval vs forgetting of object memory. Furthermore, the computational modelling that captures in a formal way how certain parameters may influence memory provides an important and testable approach to understanding forgetting.

The use of the Rescorla-Wagner model in the context of object recognition and the idea of relevance being captured in negative prediction error are novel (but see below).

The use of gain and loss of function approaches are a considerable strength and the dissociable effects on behaviour eliminate the possibility of extraneous variables such as light artifacts as potential explanations for the effects.

We thank the Reviewer for their positive comments.

Weaknesses:

Knowing what process (object retrieval vs familiarity) governed the behavioural effect in the present investigation would have been of even greater significance.

The Reviewer touches on an important issue of the object recognition task. Understanding how experience alters object familiarity versus object retrieval and its impact on learning would help to develop better models of object memory and forgetting. We have added additional discussion. See lines 666-669.

The impact of the paper is somewhat limited by the use of only one sex.

We agree that using only male mice limits the impact of the paper. Indeed, the field of behavioural neuroscience is moving to include sex as a variable. Future experiments should include both male and female mice.

While relevance is an interesting concept that has been operationalized in the paper, it is unclear how distinct it is from extinction. Specifically, in the case where the animals are exposed to the context in the absence of the object, the paper currently expresses this as a process of relevance - the objects are no longer relevant in that context. Another way to think about this is in terms of extinction - the association between the context and the objects is reduced results in a disrupted ability of the context to activate the object engram.

We thank the reviewer for their insightful comment on the connection between engram relevance and memory extinction. Lacagnina et al., demonstrated that extinction training suppressed the reactivation of a fear engram, while activating a second putative extinction ensemble (59). In another study, these extinction engram cells and reward cells were shown to be functionally interchangeable (92). Moreover, in a study conducted by Lay et al., the balance between extinction and acquisition was disrupted by inhibiting the extinction recruited neurons in the BLA and CN (93). These results suggested that decision making after extinction can be governed by a balance between acquisition and extinction specific ensembles (93). Together, this may suggest that in the present study, when mice are repeatedly exposed to the training context, the association between the context and the objects is reduced, resulting in a disrupted ability of the context to activate the object engram. Therefore, memory relevance and extinction may operate similarly to effect engram accessibility, and in essence ‘forgetting’ of object memories may be due to neurobiological mechanisms similar to that of extinction learning (4). We have included additional discussion on the link between our results and the extinction literature. See lines 642-654.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Additional measures that may help interpretation of and clarify data are:

A minute-by-minute analysis for training and testing may provide insight about the learning rate and testing temporal dynamics that may shed light substantially on differential levels of exploration. This should be applied across figures and would support conclusions from models in Figures 7-8 as well.

Locomotion/distance travelled measures.

We have included additional analysis for a minute-by-minute analysis of training and testing of the object memory test at 24 hr, 2 weeks as well as under the standard housing and enrichment conditions. The results further support the initial finding that novel object recognition is increased in mice that recall the object at 24 hr. Similarly, mice housed in the enriched housing initially explore the novel object more compared to the familiar object. See Supplementary Figure 1 and 2, as well as lines 103-105 and 211-213.

The appropriate control for the context exposure figure would be to expose to a novel context in one group and the acquisition/testing context for the other.

We agree with the reviewer that an additional control of a novel context would further support our findings. Indeed, this line of investigate may dove-tail with the other reviewer comments on the role of competing engrams and interference. Future work could investigate the degree to which novel contexts and multiple memories can affect the rate of forgetting through engram updating. We have included additional discussion. See lines 643 and 655. However, in our experience it is necessary to pre-expose mice to different contexts before object exposure (e.g. Autore et al ’23), in order to form discriminate object/context associations. Establishing such a paradigm for this study would be at odds with the established paradigms and schedules in this current study. Moreover, the possibility that the effect of object displacement on forgetting requires the familiar context, or not, does not impact the main conclusions of this study. However, we agree that it is a point for expansion in the future.

A control virus+light group vs simply a no-light condition.

For optogenetic experiments. Control mice underwent the same surgery procedure with virus and optic fibre implantation. However, no light was delivered to excite or inhibit the respective opsin. Previous papers have shown laser light delivered to tissue expressing an AAV-TRE-EYFP lacking an light-opsin does cause cellular excitation. We have clarified this in the text. See lines 726-729.

Reviewer #2 (Recommendations For The Authors):

Minor details:

(1) In the pharmacological modification of Rac 1, please specify what percentage of DMSO was used to dissolve Rac1 inhibitor and correct the typo 'DSMO'

Rac1 inhibitor (Ehop016) was reconstituted and prepared in PBS with 1% Tween-80, 1% DMSO and 30% PEG. We have clarified this in the text and corrected the typo, thank you. See lines 767.

(2) In the penultimate paragraph there is a typo 'predication error'

This is now corrected. Thankyou.

Reviewer #3 (Recommendations For The Authors):

I was unable to find information on what the No Light group consisted of. Was there a control virus infused, were the animals implanted with optical fibres (in the presence or absence of a virus), were they surgical controls, etc?

For optogenetic experiments. No Light Control mice underwent the same surgery procedure with virus and optic fibre implantation. However, no light was delivered to excite or inhibit the respective opsin. We have clarified this in the text. See lines 726-729.

The discussion lacked specificity in places. For example, the idea of eluding to 'other variables' is somewhat vague (p. 21, middle paragraph). Some examples of what other variables could be relevant would be helpful in capturing what direction or relevance the model may have going forward.

We have expanded the discussion of other variables which might impact engram relevance and how the model might be developed moving forward. These may include, boundary conditions of destabilization and reconsolidation, the salience or strength of the memory as well as the timing of retrieval cues or updating experience. Future models could focus on understanding the specific boundary conditions in which a memory becomes retrievable and the degree to which it is sufficiently destabilized and liable for updating and forgetting. The role of perceptual learning on memory retrieval and forgetting may also be an avenue of future investigation. Understanding how experience alters object familiarity versus object retrieval and its impact on learning would also help to develop better models of object memory and forgetting. In the current study, only male mice were utilized. Therefore, future work could also include sex as a variable to fully elucidate the impact of experience on the processes of forgetting. See lines 642-669.

In the same paragraph (p. 21, middle paragraph) there is mention of multiple engrams and how they can compete. The authors reference Autore et al (2023), but I thought Lacagina did this really beautifully also in an experimental setting. This idea is also expressed in Lay et al. (2022). So additional references would further strengthen the authors argument here.

We thank the reviewer for the additional references for discussing engram competition. We have included these papers in the discission. See lines 642-654.

Relatedly, environmental enrichment was considered in terms of object relevance. I wonder if the authors may want to consider thinking about their results in terms of effects on perceptual learning.

Indeed, perceptual learning maybe playing a role in environmental enrichment. We have included additional discussion. See lines 666-669.

eLife assessment

This important study evaluates a model for multisensory correlation detection, focusing on the detection of correlated transients in visual and auditory stimuli. Overall, the experimental design is sound and the evidence is compelling. The synergy between the experimental and theoretical aspects of the paper is strong, and the work will be of interest to both neuroscientists and psychologists working in the domain of sensory processing and perception.

Reviewer #1 (Public Review):

The authors present a model for multisensory correlation detection that is based on the neurobiologically plausible Hassenstein Reichardt detector (Parise & Ernst, 2016). They demonstrate that this model can account for human behaviour in synchrony or temporal order judgements and related temporal tasks in two new data sets (acquired in this study) and a range of previous data sets. While the current study is limited to the model assessment for relatively simple audiovisual signals, in future communications, the authors demonstrate that the model can also account for audiovisual integration of complex naturalistic signals such as speech and music.

The significance of this work lies in its ability to explain multisensory perception using fundamental neural mechanisms previously identified in insect motion processing.

Strengths:

(1) The model goes beyond descriptive models such as cumulative Gaussians for TOJ and differences in cumulative Gaussians for SJ tasks by providing a mechanism that builds on the neurobiologically plausible Hassenstein-Reichardt detector.<br /> (2) This model can account for results from two new experiments that focus on the detection of correlated transients and frequency doubling. The model also accounts for several behavioural results from experiments including stochastic sequences of A/V events and sine wave modulations (and naturalistic Av signals such as speech and music as shown in future communications).

Reviewer #2 (Public Review):

Summary:

This is an interesting and well-written manuscript that seeks to detail performance on two human psychophysical experiments designed to look at the relative contributions of transient and sustained components of a multisensory (i.e., audiovisual) stimulus to their integration. The work is framed within the context of a model previously developed by the authors and now somewhat revised to better incorporate the experimental findings. The major takeaway from the paper is that transient signals carry the vast majority of the information related to the integration of auditory and visual cues, and that the Multisensory Correlation Detector (MCD) model not only captures the results of the current study, but is also highly effective in capturing the results of prior studies focused on temporal and causal judgments.

Strengths:

Overall the experimental design is sound and the analyses well performed. The extension of the MCD model to better capture transients make a great deal of sense in the current context, and it is very nice to see the model applied to a variety of previous studies.

Comments on the revised version:

In the revised manuscript, the authors have done an excellent job of responding to the prior critiques. I have no additional concerns or comments.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The authors present a model for multisensory correlation detection that is based on the neurobiologically plausible Hassenstein Reichardt detector. It modifies their previously reported model (Parise & Ernst, 2016) in two ways: a bandpass (rather than lowpass) filter is initially applied and the filtered signals are then squared. The study shows that this model can account for synchrony judgement, temporal order judgement, etc in two new data sets (acquired in this study) and a range of previous data sets.

Strengths:

(1) The model goes beyond descriptive models such as cumulative Gaussians for TOJ and differences in cumulative Gaussians for SJ tasks by providing a mechanism that builds on the neurobiologically plausible Hassenstein-Reichardt detector.

(2) This modified model can account for results from two new experiments that focus on the detection of correlated transients and frequency doubling. The model also accounts for several behavioural results from experiments including stochastic sequences of A/V events and sine wave modulations.

Additional thoughts:

(1) The model introduces two changes: bandpass filtering and squaring of the inputs. The authors emphasize that these changes allow the model to focus selectively on transient rather than sustained channels. But shouldn't the two changes be introduced separately? Transients may also be detected for signed signals.

We updated the original model because our new psychophysical evidence demonstrates the fundamental role of unsigned transient for multisensory perception. While the original model received input from sustained unimodal channels (low-pass filters), the new version receives input from unsigned unimodal transient channels. Transient channels are normally modelled through bandpass filters (to remove the DC and high-frequency signal components) and squaring (to remove the sign). While these may appear as two separate changes in the model, they are, in fact, a single one: the substitution of sustained with unsigned transient channels (for a similar approach, see Stigliani et al. 2017, PNAS). Either change alone would not be sufficient to implement a transient channel that accounts for the present results.

That said, we were also concerned with introducing too many changes in the model at once. Indeed, we simply modelled the unimodal transient channels as a single band-pass filter followed by squaring. This is already a stripped-down version of the unsigned transient detectors proposed by Adelson and Bergen in their classic Motion Energy model. The original model consisted of two biphasic temporal filters 90 degrees out of phase (i.e., quadrature filters), whose output is later combined. While a simpler implementation of the transient channels was sufficient in the present study, the full model may be necessary for other classes of stimuli (including speech, Parise, 2024, BiorXiv). Therefore, for completeness, we now include in the Supplementary Information a formal description of the full model, and validate it by simulating our two novel psychophysical studies. See Supplementary Information “The quadrature MCD model” section and Supplementary Figure S8.

(2) Because the model is applied only to rather simple artificial signals, it remains unclear to what extent it can account for AV correlation detection for naturalistic signals. In particular, speech appears to rely on correlation detection of signed signals. Can this modified model account for SJ or TOJ judgments for naturalistic signals?

It can. In a recent series of studies we have demonstrated that a population of spatially-tuned MCD units can account for audiovisual correlation detection for naturalistic stimuli, including speech (e.g. the McGurk Illusion). Once again, unsigned transients were sufficient to replicate a variety of previous findings. We have now extended the discussion to cover this recent research: Parise, C. V. (2024). Spatiotemporal models for multisensory integration. bioRxiv, 2023-12.

Even Nidiffer et al. (2018) which is explicitly modelled by the authors report a significant difference in performance for correlated and anti-correlated signals. This seems to disagree with the results of study 1 reported in the current paper and the model's predictions. How can these contradicting results be explained? If the brain detects correlation on signed and unsigned signals, is a more complex mechanism needed to arbitrate between those two?

We believe the reviewer here refers to our Experiment 2 (where, like Nidiffer at al. (2018) we used periodic stimuli, not Experiment 1, which consists of step stimuli). We were also puzzled by the difference between our Experiment 2 and Nidiffer et al. (2018): we induced frequency doubling, Nidiffer did not. Based on quantitative simulations, we concluded that this difference could be attributed to the fact that while Nidiffer included on each trial an intensity ramp in their periodic audiovisual stimuli, we did not. As a result, when considering the ramp (unlike in Nidiffer’s analyses), all audiovisual signals used by Nidiffer were positively correlated (irrespective of frequency and phase offset), while our signals in Experiment 2 were sometimes correlated and other times not (depending on the phase offset). This important simulation is included in Supplementary Figure S7; we also have now updated the text to better highlight the role of the pedestal in determining the direction of the correlation.

(3) The number of parameters seems quite comparable for the authors' model and descriptive models (e.g. PSF models). This is because time constants require refitting (at least for some experimental data sets) and the correlation values need to be passed through a response mode (i.e. probit function) to account for behavioural data. It remains unclear how the brain adjusts the time constants to different sensory signals.

This is a deep question. For simplicity, here the temporal constants were fitted to the empirical psychometric functions. To avoid overfitting, whenever possible we fitted such parameters over some training datasets, while trying to predict others. However, in some cases, it was necessary to fit the temporal constants to specific datasets. This may suggest that the temporal tuning of those units is not crystalised to some pre-defined values, but is adjusted based on recent perceptual history (e.g., the sequence of trials and stimuli participants are exposed to during the various experiments).

For transparency, here we show how varying the tuning of the temporal constants of the filters affects the goodness of fit of our new psychophysical experiments (Supplementary Figure S8). As it can be readily appreciated, the relative temporal tuning of the unimodal transient detector was critical, though their absolute values could vary over a range of about 15 to over 100ms. The tuning of the low-pass filters of the correlation detector (not shown here) displayed much lower temporal sensitivity over a range between 0.1s to over 1s.

This simulation shows the impact of temporal tuning in our simulations, however, the question remains as to how such a tuning gets selected in the first place. An appealing explanation relies on natural scene statistics: units are temporally tuned to the most common audiovisual stimuli. Although our current empirical evidence does not allow us to quantitatively address this question, in previous simulations (see Parise & Ernst, 2016, Supplementary Figure 8), by analogy with visual motion adaptation, we show how the temporal constants of our model can dynamically adjust and adapt to recent perceptual history. We hope these new and previous simulations address the question about the nature of the temporal tuning of the MCD units.

(4) Fujisaki and Nishida (2005, 2006) proposed mechanisms for AV correlation detection based on the Hassenstein-Reichardt motion detector (though not formalized as a computational model).

This is correct, Fujisaki and Nishida (2005, 2007) also hypothesized that AV synchrony could be detected using a mechanism analogous to motion detection. Interestingly, however, they ruled out such a hypothesis, as their “data do not support the existence of specialized low-level audio-visual synchrony detectors”. Yet, along with our previous work (Parise & Ernst, 2016, where we explicitly modelled the experiments of Fujisaki and Nishida), the present simulations quantitatively demonstrate that a low-level AV synchrony detector is instead sufficient to account for audiovisual synchrony perception and correlation detection. We now credit Fujusaki and Nishida in the modelling section for proposing that AV synchrony can be detected by a cross-correlator.

Finally, we believe the reviewer is referring to the 2005 and 2007 studies of Fujisaki and Nishida (not 2006); here are the full references of the two articles we are referring to:

Fujisaki, W., & Nishida, S. Y. (2005). Temporal frequency characteristics of synchrony–asynchrony discrimination of audio-visual signals. Experimental Brain Research, 166, 455-464.

Fujisaki, W., & Nishida, S. Y. (2007). Feature-based processing of audio-visual synchrony perception revealed by random pulse trains. Vision Research, 47(8), 1075-1093.

Reviewer #2 (Public Review):

Summary:

This is an interesting and well-written manuscript that seeks to detail the performance of two human psychophysical experiments designed to look at the relative contributions of transient and sustained components of a multisensory (i.e., audiovisual) stimulus to their integration. The work is framed within the context of a model previously developed by the authors and is now somewhat revised to better incorporate the experimental findings. The major takeaway from the paper is that transient signals carry the vast majority of the information related to the integration of auditory and visual cues, and that the Multisensory Correlation Detector (MCD) model not only captures the results of the current study but is also highly effective in capturing the results of prior studies focused on temporal and causal judgments.

Strengths:

Overall the experimental design is sound and the analyses are well performed. The extension of the MCD model to better capture transients makes a great deal of sense in the current context, and it is very nice to see the model applied to a variety of previous studies.

Weaknesses:

My one major issue with the paper revolves around its significance. In the context of a temporal task(s), is it in any way surprising that the important information is carried by stimulus transients? Stated a bit differently, isn't all of the important information needed to solve the task embedded in the temporal dimension? I think the authors need to better address this issue to punch up the significance of their work.

In hindsight, it may appear unsurprising that transient signals carry most information for audiovisual integration. Yet, so somewhat unexpectedly, this has never been investigated using perhaps the most diagnostic psychophysical tools for perceived crossmodal timing; namely temporal order and simultaneity judgments–along with carefully designed experiments with quantitative predictions for the effect of either channel. The fact that the results conform to intuitive expectations further supports the value of the present work: grounding empirically with what is intuitively expected. This offers solid psychophysical evidence that one can build on for future advancements. Importantly, developing a model that builds on our new results and uses the same parameters to predict a variety of classic experiments in the field, further supports the current approach.

If “significance” is intended as shaking previous intuitions or theories, then no: this is not a significant contribution. If instead, by significance we intend to build a solid empirical and theoretical ground for future work, then we believe this study is not significant, it is foundational. We hope that this work's significance is better captured in our discussion.

On a side note, there is an intriguing factor around transient vs. sustained channels: what matters is the amount of change, not the absolute stimulus intensity. Previous studies, for example, have suggested a positive cross modal mapping between auditory loudness and visual lightness or brightness [Odegaard et al., 2004]. This study, conversely, challenges this view and demonstrates that what matters for multisensory integration in time is not the intensity of a stimulus, but changes thereof.

In a more minor comment, I think there also needs to be a bit more effort into articulating the biological plausibility/potential instantiations of this sustained versus transient dichotomy. As written, the paper suggests that these are different "channels" in sensory systems, when in reality many neurons (and neural circuits) carry both on the same lines.

The reviewer is right, in our original manuscript we glossed over this aspect. We have now expanded the introduction to discuss their anatomical basis. However, we are not assuming any strict dichotomy between transient and sustained channels; rather, our results and simulations demonstrate that transient information is sufficient to account for audiovisual temporal integration.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Related to point 2 of the public review, can the authors provide additional results showing that the model can also account for naturalistic signals and more complex stochastic signals?

While working on this manuscript, we were also working in parallel on a project related to audiovisual integration of naturalistic signals. A pre-print is available online [Parise, 2024, BiorXiv], and the related study is now discussed in the conclusions.

(2) As noted in the public review, Fujisaki and Nishida (2005, 2006) already proposed mechanisms for AV correlation detection based on the Hassenstein-Reichardt motion detector. Their work should be referenced and discussed.

We have now acknowledged the contribution of Fujisaki and Nishida in the modelling section, when we first introduce the link between our model and the Hassenstein-Reichardt detectors.

(3) Experimental parameters: Was the phase shift manipulated in blocks? If yes, what about temporal recalibration?

To minimise the effect of temporal recalibration, the order of trials in our experiments was randomised. Nonetheless, we can directly assess potential short-term recalibration effects by plotting our psychophysical responses against both the current SOA, and that of the previous trials. The resulting (raw) psychometric surfaces below are averaged across observers (and conditions for Experiment 1). In all our experiments, responses are obviously dependent on the current SOA (x-axis). However, the SOA of the previous trials (y-axis) does not seem to meaningfully affect simultaneity and temporal order judgments. The psychometric curves above the heatmaps represent the average psychometric functions (marginalized over the SOA of the previous trial).

All in all, the present analyses demonstrate negligible temporal recalibration across trials, likely induced by a random sequence of lags or phase shifts. Therefore, when estimating the temporal constants of the model, it seems reasonable to ignore the potential effects of temporal recalibration. To avoid increasing the complexity of the present manuscript, we would prefer not to include the present analyses in the revised version.

Author response image 1.

Effect of previous trial. Psychometric surfaces for Experiments 1 and 2 plotted against the lag in the current vs. the previous trial. While psychophysical responses are strongly modulated by the lag in the last trial (horizontal axis), they are relatively unaffected by the lag in the previous trial (vertical axis).

(4) The model predicts no differences for experiment 1 and this is what is empirically observed. Can the authors support these null results with Bayes factors?

This is a good suggestion: we have now included a Bayesian repeated measures ANOVA to the analyses of Experiment 1. As expected, these analyses provide further, though mild evidence in support for the null hypothesis (See Table S2). For completeness, the new Bayesian analyses are presented alongside the previous frequentist ones in the revised manuscript.

eLife assessment

The authors combined neurophysiological (electroencephalography [EEG]) and neurochemical (magnetic resonance spectroscopy [MRS]) measures to empirically evaluate the neural noise hypothesis of developmental dyslexia. Their results are solid, supported by consistent findings from the two complementary methodologies and Bayesian statistics. Additional analyses, particularly on the neurochemical measures, are necessary to further substantiate the results. This study is useful for understanding the neural mechanisms of dyslexia and neural development in general.

Reviewer #1 (Public Review):

Summary:

"Neural noise", here operationalized as an imbalance between excitatory and inhibitory neural activity, has been posited as a core cause of developmental dyslexia, a prevalent learning disability that impacts reading accuracy and fluency. This study is the first to systematically evaluate the neural noise hypothesis of dyslexia. Neural noise was measured using neurophysiological (electroencephalography [EEG]) and neurochemical (magnetic resonance spectroscopy [MRS]) in adolescents and young adults with and without dyslexia. The authors did not find evidence of elevated neural noise in the dyslexia group from EEG or MRS measures, and Bayes factors generally informed against including the grouping factor in the models. Although the comparisons between groups with and without dyslexia did not support the neural noise hypothesis, a mediation model that quantified phonological processing and reading abilities continuously revealed that EEG beta power in the left superior temporal sulcus was positively associated with reading ability via phonological awareness. This finding lends support for analysis of associations between neural excitatory/inhibitory factors and reading ability along a continuum, rather than as with a case/control approach, and indicates the relevance of phonological awareness as an intermediate trait that may provide a more proximal link between neurobiology and reading ability. Further research is needed across developmental stages and over a broader set of brain regions to more comprehensively assess the neural noise hypothesis of dyslexia, and alternative neurobiological mechanisms of this disorder should be explored.

Strengths:

The inclusion of multiple methods of assessing neural noise (neurophysiological and neurochemical) is a major advantage of this paper. MRS at 7T confers an advantage of more accurately distinguishing and quantifying glutamate, which is a primary target of this study. In addition, the subject-specific functional localization of the MRS acquisition is an innovative approach. MRS acquisition and processing details are noted in the supplementary materials according to the experts' consensus-recommended checklist (https://doi.org/10.1002/nbm.4484). Commenting on the rigor, the EEG methods is beyond my expertise as a reviewer.

Participants recruited for this study included those with a clinical diagnosis of dyslexia, which strengthens confidence in the accuracy of the diagnosis. The assessment of reading and language abilities during the study further confirms the persistently poorer performance of the dyslexia group compared to the control group.

The correlational analysis and mediation analysis provide complementary information to the main case-control analyses, and the examination of associations between EEG and MRS measures of neural noise is novel and interesting.

The authors follow good practice for open science, including data and code sharing. They also apply statistical rigor, using Bayes Factors to support conclusions of null evidence rather than relying only on non-significant findings. In the discussion, they acknowledge the limitations and generalizability of the evidence and provide directions for future research on this topic.

Weaknesses:

Though the methods employed in the paper are generally strong, there are certain aspects that are not clearly described in the Materials & Methods section, such as a description of the statistical analyses used for hypothesis testing.

With regard to metabolite quantification, it is unclear why the authors chose to analyze and report metabolite values in terms of creatine ratios rather than quantification based on a water reference given that the MRS acquisition appears to support using a water reference. GABA is typically quantified using J-editing sequences as lower field strengths (~3T), and there is some evidence that the GABA signal can be reliably measured at 7T without editing, however, the authors should discuss potential limitations, such as reliability of Glu and GABA measurements with short-TE semi-laser at 7T. In addition, MRS measurements of GABA are known to be influenced by macromolecules, and GABA is often denoted as GABA+ to indicate that other compounds contribute to the measured signal, especially at a short TE and in the absence of symmetric spectral editing. A general discussion of the strengths and limitations of unedited Glu and GABA quantification at 7T is warranted given the interest of this work to researchers who may not be experts in MRS.

Further, the single MRS voxel location is a limitation of the study as neurochemistry can vary regionally within individuals, and the putative excitatory/inhibitory imbalance in dyslexia may appear in regions outside the left temporal cortex (e.g., network-wide or in frontal regions involved in top-down executive processes). While the functional localization of the MRS voxel is a novelty and a potential advantage, it is unclear whether voxel placement based on left-lateralized reading-related neural activity may bias the experiment to be more sensitive to small, activity-related fluctuations in neurotransmitters in the CON group vs. the DYS group who may have developed an altered, compensatory reading strategy.

As the authors note in the discussion, sex could serve as a moderator of associations between neural noise and reading abilities and should be considered in future studies.

Appraisal:

The authors present a thorough evaluation of the neural noise hypothesis of developmental dyslexia in a sample of adolescents and young adults using multiple methods of measuring excitatory/inhibitory imbalances as an indicator of neural noise. The authors concluded that there was no support for the neural noise hypothesis of dyslexia in their study based on null significance and Bayes factors. This conclusion is justified, and further research is called for to more broadly evaluate the neural noise hypothesis in developmental dyslexia.

Impact:

This study provides an exemplary foundation for the evaluation of the neural noise hypothesis of dyslexia. Other researchers may adopt the model applied in this paper to examine neural noise in various populations with/without dyslexia, or across a continuum of reading abilities, to more thoroughly examine the evidence (or lack thereof) for this hypothesis. Notably, the lack of evidence here does not rule out the possibility of a role for neural noise in dyslexia, and the authors point out that presentation with co-occurring conditions, such as ADHD, may contribute to neural noise in dyslexia. Dyslexia remains a multi-faceted and heterogenous neurodevelopmental condition, and many genetic, neurobiological, and environmental factors play a role. This study demonstrates one step toward evaluating neurobiological mechanisms that may contribute to reading difficulties.

Reviewer #2 (Public Review):

Summary:

This study utilized two complementary techniques (EEG and 7T MRI/MRS) to directly test a theory of dyslexia: the neural noise hypothesis. The authors report finding no evidence to support an excitatory/inhibitory balance, as quantified by beta in EEG and Glutamate/GABA ratio in MRS. This is important work and speaks to one potential mechanism by which increased neural noise may occur in dyslexia.

Strengths:

This is a well-conceived study with in-depth analyses and publicly available data for independent review. The authors provide transparency with their statistics and display the raw data points along with the averages in figures for review and interpretation. The data suggest that an E/I balance issue may not underlie deficits in dyslexia and is a meaningful and needed test of a possible mechanism for increased neural noise.

Weaknesses:

The researchers did not include a visual print task in the EEG task, which limits analysis of reading-specific regions such as the visual word form area, which is a commonly hypoactivated region in dyslexia. This region is a common one of interest in dyslexia, yet the researchers measured the I/E balance in only one region of interest, specific to the language network. Further, this work does not consider prior studies reporting neural inconsistency; a potential consequence of increased neural noise, which has been reported in several studies and linked with candidate-dyslexia gene variants (e.g., Centanni et al., 2018, 2022; Hornickel & Kraus, 2013; Neef et al., 2017). While E/I imbalance may not be a cause of increased neural noise, other potential mechanisms remain and should be discussed.

Reviewer #3 (Public Review):

Summary:

This study by Glica and colleagues utilized EEG (i.e., Beta power, Gamma power, and aperiodic activity) and 7T MRS (i.e., MRS IE ratio, IE balance) to reevaluate the neural noise hypothesis in Dyslexia. Supported by Bayesian statistics, their results show solid 'no evidence' of EI balance differences between groups, challenging the neural noise hypothesis. The work will be of broad interest to neuroscientists, and educational and clinical psychologists.

Strengths:

Combining EEG and 7T MRS, this study utilized both the indirect (i.e., Beta power, Gamma power, and aperiodic activity) and direct (i.e., MRS IE ratio, IE balance) measures to reevaluate the neural noise hypothesis in Dyslexia.

Weaknesses:

The authors may need to provide more data to assess the quality of the MRS data.

eLife assessment:

This valuable study investigates the oscillatory activity of gonadotropin-releasing hormone (GnRH) neurones in mice using GCaMP fiber photometry. It demonstrates three distinct patterns of oscillatory activity that occur in GnRH neurons comprising low-level rapid baseline activity, abrupt short-duration oscillations that drive pulsatile gonadotropin secretion, and, in females, a gradual and prolonged oscillating increase in activity responsible for the relatively short-lived preovulatory LH surge. The evidence presented in the study is solid, offering theoretical implications for understanding the behaviour of GnRH neurones in the context of reproductive physiology, and will be of interest to researchers in neuroendocrinology and reproductive biology.

Reviewer #1 (Public Review):

Summary:

The authors aimed to investigate the oscillatory activity of GnRH neurones in freely behaving mice. By utilising GCaMP fiber photometry, they sought to record real-time neuronal activity to understand the patterns and dynamics of GnRH neuron firing and their implications for reproductive physiology.

Strengths:

(1) The use of GCaMP fiber photometry allows for high temporal resolution recordings of neuronal activity, providing real-time data on the dynamics of GnRH neurones.

(2) Recording in freely behaving animals ensures that the findings are physiologically relevant and not artifacts of a controlled laboratory environment.

(3) The authors used statistical methods to characterise the oscillatory patterns, ensuring the reliability of their findings.

Weaknesses:

(1) While the study identifies distinct oscillatory patterns in GnRH neurones' calcium dynamics, it falls short in exploring the functional implications of these patterns for GnRH pulsatility and overall reproductive physiology.

(2) The study lacks a broader discussion to include comparisons with existing studies on GnRH neurone activity and pulsatility and highlight how the findings of this study align with or differ from previous research and what novel contributions are made.

(3) The authors aimed to characterise the oscillatory activity of GnRH neurons and successfully identified distinct oscillatory patterns. The results support the conclusion that GnRH neurons exhibit complex oscillatory behaviours, which are critical for understanding their role in reproductive physiology. However, it has not been made clear what exactly the authors mean by "multi-dimensional oscillatory patterns" and how has this been shown.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors report GCaMP fiber-photometry recordings from the GnRH neuron distal projections in the ventral arcuate nucleus. The recordings are taken from intact, male and female, freely behaving mice. The report three patterns of neuronal activity:

(1) Abrupt increases in the Ca2+ signals that are perfectly correlated with LH pulses.

(2) A gradual, yet fluctuating (with a slow ultradian frequency), increase in activity, which is associated with the onset of the LH surge in female animals.

(3) Clustered (high frequency) baseline activity in both female and male animals.

Strengths:

The GCaMP fiber-photometry recordings reported here are the first direct recordings from GnRH neurones in vivo. These recordings have uncovered a rich repertoire of activity suggesting the integration of distinct "surge" and "pulse" generation signals, and an ultradian rhythm during the onset of the surge.

Weaknesses:

The data analysis method used for the characterisation of the ultradian rhythm observed during the onset of the surge is not detailed enough. Hence, I'm left wondering whether this rhythm is in any way correlated with the clusters of activity observed during the rest of the cycle and which have similar duration.

eLife assessment

Somatostatin-expressing neurons of the entopeduncular nucleus (EPNSst+) co-release GABA and glutamate in their projection to the lateral habenula, a structure that is key for reward-based learning. Combining fiber photometry and computational modeling, the authors provide compelling evidence that EPNSst+ neural activity represents movement, choice direction, and reward outcomes in a probabilistic switching task but, surprisingly, neither chronic genetic silencing of these neurons nor selective elimination glutamate release affected behavioral performance in well-trained animals. This valuable study shows that despite its representation of key task variables, EPNSst+ neurons are dispensable for ongoing performance in a task requiring outcome monitoring to optimize reward. This study will be of interest to those interested in reward learning and/or reward-related behavior and systems or behavioral neuroscience more broadly.

Reviewer #1 (Public Review):

Summary:

In this series of studies, Locantore et al. investigated the role of SST-expressing neurons in the entopeduncular nucleus (EPNSst+) in probabilistic switching tasks, a paradigm that requires continued learning to guide future actions. In prior work, this group had demonstrated EPNSst+ neurons co-release both glutamate and GABA and project to the lateral habenula (LHb), and LHb activity is also necessary for outcome evaluation necessary for performance in probabilistic decision-making tasks. Previous slice physiology works have shown that the balance of glutamate/GABA co-release is plastic, altering the net effect of EPN on downstream brain areas and neural circuit function. The authors used a combination of in vivo calcium monitoring with fiber photometry and computational modeling to demonstrate that EPNSst+ neural activity represents movement, choice direction, and reward outcomes in their behavioral task. However, viral-genetic manipulations to synaptically silence these neurons or selectively eliminate glutamate release had no effect on behavioral performance in well-trained animals. The authors conclude that despite their representation of task variables, EPN Sst+ neuron synaptic output is dispensable for task performance.

Strengths and Weaknesses:

Overall, the manuscript is exceptionally scholarly, with a clear articulation of the scientific question and a discussion of the findings and their limitations. The analyses and interpretations are careful and rigorous. This review appreciates the thorough explanation of the behavioral modeling and GLM for deconvolving the photometry signal around behavioral events, and the transparency and thoroughness of the analyses in the supplemental figures. This extra care has the result of increasing the accessibility for non-experts, and bolsters confidence in the results. To bolster a reader's understanding of results, we suggest it would be interesting to see the same mouse represented across panels (i.e. Figures 1 F-J, Supplementary Figures 1 F, K, etc i.e via the inclusion of faint hash lines connecting individual data points across variables. Additionally, Figure 3E demonstrates that eliminating the 'reward' and 'choice and reward' terms from the GLM significantly worsens model performance; to demonstrate the magnitude of this effect, it would be interesting to include a reconstruction of the photometry signal after holding out of both or one of these terms, alongside the 'original' and 'reconstructed' photometry traces in panel D. This would help give context for how the model performance degrades by exclusion of those key terms. Finally, the authors claimed calcium activity increased following ipsilateral movements. However, Figure 3C clearly shows that both SXcontra and SXipsi increase beta coefficients. Instead, the choice direction may be represented in these neurons, given that beta coefficients increase following CXipsi and before SEipsi, presumably when animals make executive decisions. Could the authors clarify their interpretation on this point? Also, it is not clear if there is a photometry response related to motor parameters (i.e. head direction or locomotion, licking), which could change the interpretation of the reward outcome if it is related to a motor response; could the authors show photometry signal from representative 'high licking' or 'low licking' reward trials, or from spontaneous periods of high vs. low locomotor speeds (if the sessions are recorded) to otherwise clarify this point?

There are a few limitations with the design and timing of the synaptic manipulations that would improve the manuscript if discussed or clarified. The authors take care to validate the intersectional genetic strategies: Tetanus Toxin virus (which eliminates synaptic vesicle fusion) or CRISPR editing of Slc17a6, which prevents glutamate loading into synaptic vesicles. The magnitude of effect in the slice physiology results is striking. However, this relies on the co-infection of a second AAV to express channelrhodopsin for the purposes of validation, and it is surely the case that there will not be 100% overlap between the proportion of cells infected. Alternative means of glutamate packaging (other VGluT isoforms, other transporters, etc) could also compensate for the partial absence of VGluT2, which should be discussed. The authors do not perform a complimentary experiment to delete GABA release (i.e. via VGAT editing), which is understandable, given the absence of an effect with the pan-synaptic manipulation. A more significant concern is the timing of these manipulations as the authors acknowledge. The manipulations are all done in well-trained animals, who continue to perform during the length of viral expression. Moreover, after carefully showing that mice use different strategies on the 70/30 version vs the 90/10 version of the task, only performance on the 90/10 version is assessed after the manipulation. Together, the observation that EPNsst activity does not alter performance on a well-learned, 90/10 switching task decreases the impact of the findings, as this population may play a larger role during task acquisition or under more dynamic task conditions. Additional experiments could be done to strengthen the current evidence, although the limitation is transparently discussed by the authors.

Finally, intersectional strategies target LHb-projecting neurons, although in the original characterization, it is not entirely clear that the LHb is the only projection target of EPNsst neurons. A projection map would help clarify this point.

Overall, the authors used a pertinent experimental paradigm and common cell-specific approaches to address a major gap in the field, which is the functional role of glutamate/GABA co-release from the major basal ganglia output nucleus in action selection and evaluation. The study is carefully conducted, their analyses are thorough, and the data are often convincing and thought-provoking. However, the limitations of their synaptic manipulations with respect to the behavioral assays reduce generalizability and to some extent the impact of their findings.

Reviewer #2 (Public Review):

Summary:

This paper aimed to determine the role EP sst+ neurons play in a probabilistic switching task.

Strengths:

The in vivo recording of the EP sst+ neuron activity in the task is one of the strongest parts of this paper. Previous work had recorded from the EP-LHb population in rodents and primates in head-fixed configurations, the recordings of this population in a freely moving context is a valuable addition to these studies and has highlighted more clearly that these neurons respond both at the time of choice and outcome.

The use of a refined intersectional technique to record specifically the EP sst+ neurons is also an important strength of the paper. This is because previous work has shown that there are two genetically different types of glutamatergic EP neurons that project to the LHb. Previous work had not distinguished between these types in their recordings so the current results showing that the bidirectional value signaling is present in the EP sst+ population is valuable.

Weaknesses:

(1) One of the main weaknesses of the paper is to do with how the effect of the EP sst+ neurons on the behavior was assessed.

(a) All the manipulations (blocking synaptic release and blocking glutamatergic transmission) are chronic and more importantly the mice are given weeks of training after the manipulation before the behavioral effect is assessed. This means that as the authors point out in their discussion the mice will have time to adjust to the behavioral manipulation and compensate for the manipulations. The results do show that mice can adapt to these chronic manipulations and that the EP sst+ are not required to perform the task. What is unclear is whether the mice have compensated for the loss of EP sst+ neurons and whether they play a role in the task under normal conditions. Acute manipulations or chronic manipulations without additional training would be needed to assess this.

(b) Another weakness is that the effect of the manipulations was assessed in the 90/10 contingency version of the task. Under these contingencies, mice integrate past outcomes over fewer trials to determine their choice and animals act closer to a simple win-stay-lose switch strategy. Due to this, it is unclear if the EP sst+ neurons would play a role in the task when they must integrate over a larger number of conditions in the less deterministic 70/30 version of the task.

The authors show an intriguing result that the EP sst+ neurons are excited when mice make an ipsilateral movement in the task either toward or away from the center port. This is referred to as a choice response, but it could be a movement response or related to the predicted value of a specific action. Recordings while mice perform movement outside the task or well-controlled value manipulations within the session would be needed to really refine what these responses are related to.

(2) The authors conclude that they do not see any evidence for bidirectional prediction errors. It is not possible to conclude this. First, they see a large response in the EP sst+ neurons to the omission of an expected reward. This is what would be expected of a negative reward prediction error. There are much more specific well-controlled tests for this that are commonplace in head-fixed and freely moving paradigms that could be tested to probe this. The authors do look at the effect of previous trials on the response and do not see strong consistent results, but this is not a strong formal test of what would be expected of a prediction error, either a positive or negative. The other way they assess this is by looking at the size of the responses in different recording sessions with different reward contingencies. They claim that the size of the reward expectation and prediction error should scale with the different reward probabilities. If all the reward probabilities were present in the same session this should be true as lots of others have shown for RPE. Because however this data was taken from different sessions it is not expected that the responses should scale, this is because reward prediction errors have been shown to adaptively scale to cover the range of values on offer (Tobler et al., Science 2005). A better test of positive prediction error would be to give a larger-than-expected reward on a subset of trials. Either way, there is already evidence that responses reflect a negative prediction error in their data and more specific tests would be needed to formally rule in or out prediction error coding especially as previous recordings have shown it is present in previous primate and rodent recordings.

(3) There are a lot of variables in the GLM that occur extremely close in time such as the entry and exit of a port. If two variables occur closely in time and are always correlated it will be difficult if not impossible for a regression model to assign weights accurately to each event. This is not a large issue, but it is misleading to have regression kernels for port entry and exits unless the authors can show these are separable due to behavioral jitter or a lack of correlation under specific conditions, which does not seem to be the case.

Reviewer #3 (Public Review):

Summary:

The authors find that Sst-EPN neurons, which project to the lateral habenula, encode information about response directionality (left vs right) and outcome (rewarded vs unrewarded). Surprisingly, impairment of vesicular signaling in these neurons onto their LHb targets did not impair probabilistic choice behavior.

Strengths:

Strengths of the current work include extremely detailed and thorough analysis of data at all levels, not only of the physiological data but also an uncommonly thorough analysis of behavioral response patterns.

Weaknesses:

Overall, I saw very few weaknesses, with only two issues, both of which should be possible to address without new experiments:

(1) The authors note that the neural response difference between rewarded and unrewarded trials is not an RPE, as it is not affected by reward probability. However, the authors also show the neural difference is partly driven by the rapid motoric withdrawal from the port. Since there is also a response component that remains different apart from this motoric difference (Figure 2, Supplementary Figure 1E), it seems this is what needs to be analyzed with respect to reward probability, to truly determine whether there is no RPE component. Was this done?

(2) The current study reaches very different conclusions than a 2016 study by Stephenson-Jones and colleagues despite using a similar behavioral task to study the same Sst-EPN-LHb circuit. This is potentially very interesting, and the new findings likely shed important light on how this circuit really works. Hence, I would have liked to hear more of the authors' thoughts about possible explanations of the differences. I acknowledge that a full answer might not be possible, but in-depth elaboration would help the reader put the current findings in the context of the earlier work, and give a better sense of what work still needs to be done in the future to fully understand this circuit.

For example, the authors suggest that the Sst-EPN-LHb circuit might be involved in initial learning, but play less of a role in well-trained animals, thereby explaining the lack of observed behavioral effect. However, it is my understanding that the probabilistic switching task forces animals to continually update learned contingencies, rendering this explanation somewhat less persuasive, at least not without further elaboration (e.g. maybe the authors think it plays a role before the animals learn to switch?).

Also, as I understand it, the 2016 study used manipulations that likely impaired phasic activity patterns, e.g. precisely timed optogenetic activation/inhibition, and/or deletion of GABA/glutamate receptors. In contrast, the current study's manipulations - blockade of vesicle release using tetanus toxin or deletion of VGlut2, would likely have blocked both phasic and tonic activity patterns. Do the authors think this factor, or any others they are aware of, could be relevant?

Author response:

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

Reviewer #1 (Public Review):

Summary:

This important work advances our understanding of sperm motility regulation during fertilization by uncovering the midpiece/mitochondria contraction associated with motility cessation and structural changes in the midpiece actin network as its mode of action. The evidence supporting the conclusion is solid, with rigorous live cell imaging using state-of-the-art microscopy, although more functional analysis of the midpiece/mitochondria contraction would have further strengthened the study. The work will be of broad interest to cell biologists working on the cytoskeleton, mitochondria, cell fusion, and fertilization. Strengths: The authors demonstrate that structural changes in the flagellar midpiece F-actin network are concomitant to midpiece/mitochondrial contraction and motility arrest during sperm-egg fusion by rigorous live cell imaging using state-of-art microscopy.

Response P1.1: We thank the reviewer for her/his positive assessment of our manuscript.

Weaknesses:

Many interesting observations are listed as correlated or in time series but do not necessarily demonstrate the causality and it remains to be further tested whether the sperm undergoing midpiece contraction are those that fertilize or those that are not selected. Further elaboration of the function of the midpiece contraction associated with motility cessation (a major key discovery of the manuscript) would benefit from a more mechanistic study.

Response P1.2: We thank the reviewer for this point. We have toned down some of our statements since some of the observations are indeed temporal correlations. We will explore some of these possible connections in future experiments. In addition, we have now incorporated additional experiments and possible explanations about the function of the midpiece contraction.

Reviewer #2 (Public Review): 

(1) The authors used various microscopy techniques, including super-resolution microscopy, to observe the changes that occur in the midpiece of mouse sperm flagella. Previously, it was shown that actin filaments form a double helix in the midpiece. This study reveals that the structure of these actin filaments changes after the acrosome reaction and before sperm-egg fusion, resulting in a thinner midpiece. Furthermore, by combining midpiece structure observation with calcium imaging, the authors show that changes in intracellular calcium concentrations precede structural changes in the midpiece. The cessation of sperm motility by these changes may be important for fusion with the egg. Elucidation of the structural changes in the midpiece could lead to a better understanding of fertilization and the etiology of male infertility. The conclusions of this manuscript are largely supported by the data, but there are several areas for improvement in data analysis and interpretation. Please see the major points below.

Response P2.1: We thank the reviewer for the positive comments.

(2) It is unclear whether an increased FM4-64 signal in the midpiece precedes the arrest of sperm motility. in or This needs to be clarified to argue that structural changes in the midpiece cause sperm motility arrest. The authors should analyze changes in both motility and FM4-64 signal over time for individual sperm.

Response P2.2 : We have conducted single cell experiments tracking both FM4-64 and motility as the reviewer suggested (Supplementary Fig S1). We have observed that in all cases, cells gradually diminished the beating frequency and increased FM4-64 fluorescence in the midpiece until a complete motility arrest is observed. A representative example is shown in this Figure but we will reinforce this concept in the results section.

(3) It is possible that sperm stop moving because they die. Figure 1G shows that the FM464 signal is increased in the midpiece of immotile sperm, but it is necessary to show that the FM4-64 signal is increased in sperm that are not dead and retain plasma membrane integrity by checking sperm viability with propidium iodide or other means.

Response P2.3: This is a very good point. In our experiments, we always considered sperm that were motile to hypothesize about the relevance of this observation. We have two types of experiments: 

(1) Sperm-egg Fusion: In experiments where sperm and eggs were imaged to observe their fusion, sperm were initially moving and after fusion, the midpiece contraction (increase in FM4-64 fluorescence was observed) indicating that the change in the midpiece (that was observed consistently in all fusing cells analyzed), is part of the process. 

(2) Sperm that underwent acrosomal exocytosis (AE): we have observed two behaviours as shown in Figure 1: 

a) Sperm that underwent AE and they remain motile without midpiece contraction (they are alive for sure); 

b) Sperm that underwent AE and stopped moving with an increase in FM464 fluorescence. We propose that this contraction during AE is not desired because it will impede sperm from moving forward to the fertilization site when they are in the female reproductive tract. In this case, we acknowledge that the cessation of sperm motility may be attributed to cellular death, potentially correlating with the increased FM4-64 signal observed in the midpiece of immotile sperm that have undergone AE. To address this hypothesis, we conducted image-based flow cytometry experiments, which are well-suited for assessing cellular heterogeneity within large populations.

Author response image 1 illustrates the relationship between cell death and spontaneous AE in noncapacitated mouse sperm, where intact acrosomes are marked by EGFP. Cell death was evaluated using Sytox Blue staining, a dye that is impermeable to live cells and shows affinity for DNA. AE was assessed by the absence of EGFP in the acrosome. 

Author response image 1a indicates a lack of correlation between Sytox and EGFP fluorescence. Two populations of sperm with EGFP signals were found (EGFP+ and EGFP-), each showing a broad distribution of Sytox signal, enabling the distinction between cells that retain plasma membrane integrity (live sperm: Sytox-) and those with compromised membranes (dead cells: Sytox+). The observed bimodal distribution of EGFP signal, regardless of live versus dead cell populations, indicates that the fenestration of the plasma membrane known to occur during AE is a regulated process that does not necessarily compromise the overall plasma membrane integrity. 

These observations are reinforced by the single-cell examples in Author response image 1b, where we were able to identify sperm in four categories: live sperm with intact acrosome (EGFP+/Sytox-), live sperm with acrosomal exocytosis (EGFP-/Sytox-), dead sperm with intact acrosome (EGFP+/Sytox+), and dead sperm with AE (EGFP-/Sytox+). Note the case of AE (lacking EGFP signal) which bears an intact plasma membrane (lacking Sytox Blue signal). Author response image 2 shows single-cell examples of the four categories observed with confocal microscopy to reinforce the observations from Author response image 1a.

Author response image 1.

Fi. Image based flow cytometry analysis (ImageStream Merk II), of non-capacitated mouse sperm, showing the distribution of EGFP signal (acrosome integrity) against Sytox Blue staining (cell viability).  (A) The quadrants show: Sytox Blue + / EGFP low (17.6%), Sytox Blue + / EGFP high (40.1%), Sytox Blue - / EGFP high (20.2%), and Sytox Blue - / EGFP low (21.7%). Each quadrant indicates the percentage of the total sperm population exhibiting the corresponding staining pattern. Axes are presented in a log10 scale of arbitrary units of fluorescence.  (B) Representative single-cell images corresponding to the four categorized sperm populations from the flow cytometry analysis in panel (A). The top row displays sperm with compromised plasma membrane integrity (Sytox Blue +), showing low (left) and high (right) EGFP signals. The bottom row shows sperm with intact plasma membrane (Sytox Blue -), displaying high (left) and low (right) EGFP signal. It is worth noting that when analyzing the percentages in (A), we observed that the data also encompass a population of headless flagella, which was present in all observed categories. Therefore, the percentages should be interpreted with caution.

Author response image 2.

Confocal Microscopy Examples of AE and cell viability. The top row features sperm with compromised plasma membrane integrity (Sytox Blue +) and high EGFP expression; the second row displays sperm with compromised membrane and low EGFP expression; the third row illustrates sperm with intact membrane (Sytox Blue -) and high EGFP expression; the bottom row shows sperm with intact membrane and low EGFP expression. 

Author response images 3-5 provide insight into the relationship between FM4-64 and Sytox Blue fluorescence intensities in non-capacitated sperm (CTRL, Author response image 3), capacitated sperm and acrosome exocytosis events stimulated with 100 µM progesterone (PG, Author response image 4), and capacitated sperm stimulated with 20 µM ionomycin (IONO, Author response image 5). Two populations of sperm with Sytox Blue signals were clearly distinguished (Sytox+ and Sytox-), enabling the discernment between live and dead sperm. Interestingly, the upper right panels of Author response images 3A, 4A, and 5A (Sytox Blue+ / FM4-64 high) consistently show a positive correlation between FM4-64 and Sytox Blue. This observation aligns with the concern raised by Reviewer 2, suggesting that compromised membranes due to cell death provide more binding sites for FM4-64. 

Nonetheless, the lower panels of Author response images 3A, 4A and 5A (Sytox Blue-) show no correlation with FM4-64 fluorescence, indicating that this population can exhibit either low or high FM4-64 fluorescence. As expected, in stark contrast with the CTRL case, the stimulation of AE with PG or IONO in capacitated sperm increased the population of live sperm with high FM4-64 fluorescence (Sytox Blue+ / FM4-64 high: CTRL: 7.85%, PG: 8.73%, IONO: 13.5%). 

Single-cell examples are shown in Author response images 3B, 4B, and 5B, where the four categories are represented: dead sperm with low FM4-64 fluorescence (Sytox Blue+ / FM4-64 low), dead sperm with high FM4-64 fluorescence (Sytox Blue+ / FM4-64 high), live sperm with low FM4-64 fluorescence (Sytox Blue- / FM4-64 low), and live sperm with high FM4-64 fluorescence (Sytox Blue- / FM4-64 high). 

Author response image 3.

Relationship between cell death and FM4-64 fluorescence in capacitated sperm without inductor of RA. Image-based flow cytometry analysis of non-capacitated mouse sperm loaded with FM464 and Sytox Blue dyes, with one and two minutes of incubation time, respectively. (A) The quadrants show: Sytox Blue+ / FM4-64 low (13.3%), Sytox Blue+ / FM4-64 high (49.8%), Sytox Blue- / FM4-64 low (28.1%), and Sytox Blue- / FM4-64 high (7.85%). Each quadrant indicates the percentage of the total sperm population exhibiting the corresponding staining pattern. Axes are presented on a log10 scale of arbitrary units of fluorescence. (B) Representative single-cell images corresponding to the four categorized sperm populations from the flow cytometry analysis in panel (A).

Author response image 4.

Relationship between cell death and FM4-64 fluorescence capacitated sperm stimulated with progesterone. Image-based flow cytometry analysis of non-capacitated mouse sperm loaded with FM4-64 and Sytox Blue dyes, with one and two minutes of incubation time, respectively. (A) The quadrants show: Sytox Blue+ / FM4-64 low (9.04%), Sytox Blue+ / FM4-64 high (61.6%), Sytox Blue- / FM4-64 low (19.7%), and Sytox Blue- / FM4-64 high (8.73%). Each quadrant indicates the percentage of the total sperm population exhibiting the corresponding staining pattern. Axes are presented on a log10 scale of arbitrary units of fluorescence. (B) Representative single-cell images corresponding to the four categorized sperm populations from the flow cytometry analysis in panel (A)

Author response image 5.

Relationship between cell death and FM4-64 fluorescence capacitated sperm stimulated with ionomycin. Image-based flow cytometry analysis of non-capacitated mouse sperm loaded with FM464 and Sytox Blue dyes, with one and two minutes of incubation time, respectively. (A) The quadrants show: Sytox Blue+ / FM4-64 low (4.52%), Sytox Blue+ / FM4-64 high (60.6%), Sytox Blue- / FM4-64 low (20.5%), and Sytox Blue- / FM4-64 high (13.5%). Each quadrant indicates the percentage of the total sperm population exhibiting the corresponding staining pattern. Axes are presented on a log10 scale of arbitrary units of fluorescence. (B) Representative single-cell images corresponding to the four categorized sperm populations from the flow cytometry analysis in panel (A).

Based on the data presented in Author response images 1 to 6, we derive the following conclusions summarized below:

(1) There is no direct relationship between cell death (Sytox Blue-) and AE (EGFP) (Author response images 1 and 2).

(2) There is bistability in the FM4-64 fluorescent intensity. Before reaching a certain threshold, there is no correlation between FM4-64 and Sytox Blue signals, indicating no cell death. However, after crossing this threshold, the FM4-64 signal becomes correlated with Sytox Blue+ cells, indicating cell death (Author response images 4-6).

(3) The Sytox Blue- population of capacitated sperm is sensitive to AE stimulation with progesterone, leading to the expected increase in FM4-64 fluorescence.

Therefore, while the FM4-64 signal alone is not a definitive marker for either AE or cell death, it is crucial to use additional viability assessments, such as Sytox Blue, to accurately differentiate between live and dead sperm in studies of acrosome exocytosis and sperm motility. In the present work, we did not use a cell viability marker due to the complex multicolor, multidimensional fluorescence experiments. However, cell viability was always considered, as any imaged sperm was chosen based on motility, indicated by a beating flagellum. The determination of whether selected sperm die during or after AE remains to be elucidated. The results presented in Figure 2 and Supplementary S1 show examples of motile sperm that experience an increase in FM4-64 fluorescence.

All this information is added to the manuscript (Supplementary Figure 1D).

(4) It is unclear how the structural change in the midpiece causes the entire sperm flagellum, including the principal piece, to stop moving. It will be easier for readers to understand if the authors discuss possible mechanisms.

Response P2.4: As requested, we have incorporated a possible explanation in the discussion section (see line 644-656). We propose three possible hypotheses for the cessation of sperm motility, which can be attributed to the simultaneous occurrence of various events:

(1) Rapid increase in [Ca2+]i levels: A rapid increase in [Ca2+]i levels may trigger the activation of Ca2+ pumps within the flagellum. This process consumes local ATP levels, disrupting glycolysis and thereby depleting the energy required for motility.

(2) Reorganization of the actin cytoskeleton: Alterations in the actin cytoskeleton can lead to changes in the mechanical properties of the flagellum, impacting its ability to move effectively.

(3) Midpiece contraction: Contraction in the midpiece region can potentially interfere with mitochondrial function, impeding the energy production necessary for sustained motility.

(5) The mitochondrial sheath and cell membrane are very close together when observed by transmission electron microscopy. The image in Figure 9A with the large space between the plasma membrane and mitochondria is misleading and should be corrected. The authors state that the distance between the plasma membrane and mitochondria approaches about 100 nm after the acrosome reaction (Line 330 - Line 333), but this is a very long distance and large structural changes may occur in the midpiece. Was there any change in the mitochondria themselves when they were observed with the DsRed2 signal?

Response P2.5: The authors appreciate the reviewer’s observation regarding the need to correct the image in Figure 9A, as the original depiction conveys a misleading representation of the spatial relationship between the mitochondrial sheath and the plasma membrane. This figure has been corrected to accurately reflect a more realistic proximity, while keeping in mind that it is a cartoonish representation.

Regarding the comments about the distances mentioned between former lines 330 and 333, the measurement was not intended to describe the gap between the plasma membrane and the mitochondria but rather the distance between F-actin and the plasma membrane. 

Author response image 6 shows high-resolution scanning electron microscopy (SEM) of two sperm fixed with a protocol tailored to preserve plasma membranes (ref), where the insets clearly show the flagellate architecture in the midpiece with an intact plasma membrane covering the mitochondrial network. A non-capacitated sperm with an intact acrosome is shown in panel A, and a capacitated sperm that has experienced AE is shown in panel B.

Notably, the results depicted in Author response image 6 demonstrate that, irrespective of the AE status, the distance between the plasma membrane and mitochondria consistently remains less than 20 nm, thus confirming the close proximity of these structures in both physiological states. As Reviewer 2 pointed out, if there is no significant difference in the distance between the plasma membrane and mitochondria, then the observed structural changes in the actin network within the midpiece should somehow alter the actual deposition of mitochondria within the midpiece. Figure 5D-F shows that midpiece contraction is associated with a decrease in the helical pitch of the actin network; the distance between turns of the actin helix decreases from  l = 248  nm to  l = 159  nm. This implies a net change in the number of turns the helix makes per 1 µm, from 4 to 6 µm-1.

Author response image 6.

SEM image showing the proximity between plasma membrane and mitochondria. Scale bar 100 nm.

Additionally, a structural contraction can be observed in Figure 5D-F, where the radius of the helix decreases by about 50 nm. To clarify this point, we sought to measure the deposition of individual DsRed2 mitochondria using computational superresolution microscopy—FF-SRM (SRRF and MSSR), Structured Illumination Microscopy (SIM), or a combination of both (SIM + MSSR), in 2D. Author response image 7 shows that these three approaches allow the observation of individual DsRed mitochondria; however, the complexity of their 3D arrangement, combined with the limited space between mitochondria (as seen in Author response image 6), precludes a reliable estimation of mitochondrial organization within the midpiece. To overcome these challenges, we decided to study the midpiece architecture via SEM experiments on non-capacitated versus capacitated sperm stimulated with ionomycin to undergo the AE.

Author response image 7.

Organization of mitochondria observed via FF-SRM and SIM. Scale bar 2 µm. F.N: Fluorescence normalized. F: Frequency

Author response image 8 presents a single-cell comparison of the midpiece architecture in noncapacitated (NC) and acrosome-intact (AI) versus acrosome-reacted (AR) sperm, along with measurements of the midpiece diameter throughout its length. Notably, the diameter of the midpiece increases from the base of the head to more distal regions, ranging from 0.45 nm to 1.10 µm (as shown in Author response images 7 and 8). A significant correlation between the diameter of the flagellum and its curvature was observed (Author response image 9), suggesting a reorganization of the midpiece due to shearing forces. This is further exemplified in Author response images 8 and 9, which provide individual examples of this phenomenon.

Author response image 8.

Comparison of the midpiece architecture in acrosome-intact and acrosome-reacted sperm using scanning electron microscopy (SEM).

As expected, the overall diameter of the midpiece in AI sperm was larger than in AR sperm, with measurements of 0.731 ± 0.008 µm for AI and 0.694 ± 0.007 µm for AR (p = 0.013, Kruskal-Wallis test n > 100, N = 2), as shown in Author response image 10. Additionally, this Author response image 7 indicates that the reorganization of the midpiece architecture involves a change in the periodicity of the mitochondrial network, with frequencies shifting from fNC to fEA mitochondria per micron.  

Author response image 9.

Comparison of the midpiece architecture in acrosome-intact (A) and acrosome-reacted (B) sperm using scanning electron microscopy (SEM).

Collectively, the structural results presented in Figure 5 and Author response images 6 to 10 demonstrate that the AE involves a comprehensive reorganization of the midpiece, affecting its diameter, pitch, and the organization of both the actin and mitochondrial networks. All this information is now incorporated in the new version of the paper (Figure. 2F)

Author response image 10.

Quantification of the midpiece diameter of the sperm flagellum in acrosome-intact and acrosome-reacted sperm analyzed by scanning electron microscopy (SEM). Data is presented as mean ± SEM. Kruskal-Wallis test was employed,  p = 0.013 (AI n=85 , AR n=72).

(6) In the TG sperm used, the green fluorescence of the acrosome disappears when sperm die. Figure 1C should be analyzed only with live sperm by checking viability with propidium iodide or other means.

Response P2.6: We concur with Reviewer 2 that ideally, any experiment conducted for this study should include an intrinsic cell viability test. However, the current research employs a wide array of multidimensional imaging techniques that are not always compatible with, or might be suboptimal for, simultaneous viability assessments. In agreement with the reviewer's concerns, it is recognized that the data presented in Figure 1C may inherently be biased due to cell death. Nonetheless, Author response image 1 demonstrates that the relationship between AE and cell death is more complex than a straightforward all-or-nothing scenario. Specifically, Author response image 1C illustrates a case where the plasma membrane is compromised (Sytox Blue+) yet maintains acrosomal integrity (EGFP+). This observation contradicts Reviewer 1's assertion that "the green fluorescence of the acrosome disappears when sperm die," as discussed more comprehensively in response P2.3.

In light of these observations, we have meticulously revisited the entire manuscript to address and clarify potential biases in our results due to cell death. Consequently, Author response image 5 and its detailed description have been incorporated into the supplementary material of the manuscript to contribute to the transparency and reliability of our findings.

Reviewer #3 (Public Review):

(1) While progressive and also hyperactivated motility are required for sperm to reach the site of fertilization and to penetrate the oocyte's outer vestments, during fusion with the oocyte's plasma membrane it has been observed that sperm motility ceases. Identifying the underlying molecular mechanisms would provide novel insights into a crucial but mostly overlooked physiological change during the sperm's life cycle. In this publication, the authors aim to provide evidence that the helical actin structure surrounding the sperm mitochondria in the midpiece plays a role in regulating sperm motility, specifically the motility arrest during sperm fusion but also during earlier cessation of motility in a subpopulation of sperm post acrosomal exocytosis. The main observation the authors make is that in a subpopulation of sperm undergoing acrosomal exocytosis and sperm that fuse with the plasma membrane of the oocyte display a decrease in midpiece parameter due to a 200 nm shift of the plasma membrane towards the actin helix. The authors show the decrease in midpiece diameter via various microscopy techniques all based on membrane dyes, bright-field images and other orthogonal approaches like electron microscopy would confirm those observations if true but are missing. The lack of additional experimental evidence and the fact that the authors simultaneously observe an increase in membrane dye fluorescence suggests that the membrane dyes instead might be internalized and are now staining intracellular membranes, creating a false-positive result. The authors also propose that the midpiece diameter decrease is driven by changes in sperm intracellular Ca2+ and structural changes of the actin helix network. Important controls and additional experiments are needed to prove that the events observed by the authors are causally dependent and not simply a result of sperm cells dying.

Response P3.1: We appreciate the reviewer's observations and critiques. In response, we have expanded our experimental approach to include alternative methodologies such as mathematical modeling and electron microscopy, alongside further fluorescence microscopy studies. This diversified approach aims to mitigate potential interpretation artifacts and substantiate the validity of our observations regarding the contraction of the sperm midpiece. Additionally, we have implemented further control experiments to fortify the credibility and robustness of our findings, ensuring a more comprehensive and reliable set of results.

First, we acknowledge the concerns raised by Reviewer 2 regarding the interpretation of the magnitude of the observed contraction of the sperm flagellum's midpiece (see response P2.5). Specifically, we believe that the assertion that "... there is a decrease in midpiece parameter due to a 200 nm shift of the plasma membrane towards the actin helix" stated by reviewer 3 needs careful examination. We recognize that the fluorescence microscopy data provided might not conclusively support such a substantial shift. Our live cell imaging and superresolution microscopy experiments indicate that there is a significant decrease in the diameter of the sperm flagellum associated with AE. This is supported by colocalization experiments where FM4-64-stained structures (fluorescing upon binding to membranes) are observed moving closer to Sir-Actinlabeled structures (binding to F-actin). Quantitatively, Figure S5 describes the spatial shift between FM4-64 and Sir-Actin signals, narrowing from a range of 140-210 nm to 50-110 nm (considering the 2nd and 3rd quartiles of the distributions). The mean separation distance between both signals changes from 180 nm in AI cells to 70 nm in AR cells, a net shift of 110 nm. This observation suggests caution regarding the claim of a "200 nm shift of the plasma membrane towards the actin cortex." 

Moreover, the concerns raised by Reviewer #3 about the potential internalization of membrane dyes, which might create a false-positive result by staining intracellular membranes, offer an alternative mechanism to explain a shift of up to 100 nm. This perspective is also supported by the critique from Reviewer #2 regarding the substantial distance (about 100 nm) between the plasma membrane and mitochondria post-acrosome reaction:  “The authors state that the distance between the plasma membrane and mitochondria approaches about 100 nm after the acrosome reaction (…), but this is a very long distance and large structural changes may occur in the midpiece”. These insights have prompted us to refine our methodology and interpretation of the data to ensure a more accurate representation of the underlying biological processes.

Author response image 11 shows a first principles approach in two spatial dimensions to explore three scenarios where a membrane dye, such as FM4-64, stains structures at and within the midpiece of a sperm flagellum, but yet does not result in a net change of diameter. Author response image 11A-C illustrates three theoretical arrangements of fluorescent dyes: Model 1 features two rigid, parallel structures that mimic the plasma membrane surrounding the midpiece of the flagellum. Model 2 builds on Model 1 by incorporating the possibility of dye internalization into structures located near the membrane, suggesting a slightly more complex interaction with nearby membranous intracellular structures. Model 3 represents an extreme scenario where the fluorescent dyes stain both the plasma membrane and internal structures, such as mitochondrial membranes, indicating extensive dye penetration and binding. Author response image 11D-F displays the convolution of the theoretical fluorescent signals from Models 1 to 3 with the theoretical point spread function (PSF) of a fluorescent microscope, represented by a Gaussian-like PSF with a sigma of 19 pixels (approximately 300 nm). This process simulates how each model's fluorescence would manifest under microscopic observation, showing subtle differences in the spatial distribution of fluorescence among the models. Author response image 11G-I reveals the superresolution images obtained through Mean Shift Super Resolution (MSSR) processing of the models depicted in Author response image 11D-F.

By analyzing the three scenarios, it becomes clear that the signals from Models 2 and 3 shift towards the center compared to Model 1, as depicted in Author response image 11J. This shift in fluorescence suggests that the internalization of the dye and its interaction with internal structures might significantly influence the perceived spatial distribution and intensity of fluorescence, thereby impacting the interpretation of structural changes within the midpiece. Consequently, the experimentally observed contraction of up to 100 nm in  could represent an actual contraction of the sperm flagellum's midpiece, a relocalization of the FM4-64 membrane dyes to internal structures, or a combination of both scenarios.

To discern between these possibilities, we implemented a scanning electron microscopy (SEM) approach. The findings presented in Figure 5 and Author response images 7 to 9 conclusively demonstrate that the AE involves a comprehensive reorganization of the midpiece. This reorganization affects its diameter, which changes by approximately 50 nm, as well as the pitch and the organization of both the actin and mitochondrial networks. This data corroborates the structural alterations observed and supports the validity of our interpretations regarding midpiece dynamics during the AE.

Author response image 11.

Modeling three scenarios of midpiece staining with membrane fluorescent dyes.

Secondly, we wish to clarify that in some of our experiments, we have utilized changes in the intensity of FM4-64 fluorescence as an indirect measure of midpiece contraction. This approach is supported by a linear inverse correlation between these variables, as illustrated in Figure S2D. It is important to note that this observation is correlative and indirect; therefore, our data does not directly substantiate the claim that "in a subpopulation of sperm undergoing AE and sperm that fuse with the plasma membrane of the oocyte, there is a decrease in midpiece parameter due to a 200 nm shift of the plasma membrane towards the actin helix". Specifically, we have not directly measured the distance between the plasma membrane and actin cortex in experiments involving gamete fusion.

All the concerns highlighted in this Response P1.1 have been addressed and incorporated into the manuscript. This addition aims to provide comprehensive insight into the experimental observations and methodologies used, ensuring that the data is transparent and accessible for thorough review and replication.

Editor Comment:

As the authors can see from the reviews, the reviewers had quite different degrees of enthusiasm, thus discussed extensively. The major points in consensus are summarized below and it is highly recommended that the authors consider their revisions.

(1) Causality of midpiece contraction with motility arrest is not conclusively supported by the current evidence. Time-resolved imaging of FM4-64 and motility is needed and the working model needs to be revised with two scenarios - whether the sperm contracting indicates a fertilizing sperm or sperm to be degenerated.

(2) The rationale for using FM4-64 as a plasma membrane marker is not clear as it is typically used as an endo-membrane marker, which is also related to the discrepancy of Fluo-4 signal diameter vs. FM4-64 (Figure 4E). The viability of sperm with increased FM4-64 needs to be demonstrated.

(3) The mechanism of midpiece contraction in motility cessation along the whole flagellum is not discussed.

(4) The use of an independent method to support the changes in midpiece diameter/structural changes such as DsRed (transgenic) or TEM.

(5) The claim of Ca2+ change needs to be toned down.

Response Editor: We thank the editor and the reviewers for their thorough and positive assessment of our work and the constructive feedback to further improve our manuscript. Please find below our responses to the reviewers’ comments. We have addressed all these points in the current version. Briefly,

(1) Time resolved images to show the correlation between FM4-64 fluorescence increase and the motility was incorporated

(2) The rationale for using FM4-64 was added.

(3) The mechanism of midpiece contraction was discussed in the paper

(4) An independent method was included to support our conclusions (SEM and other markers not based on membrane dyes)

(5) The results related to the calcium increase were toned down.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) To claim midpiece actin polymerization/re-organization is required for AE, demonstrating that AE does not occur in the presence of actin depolymerizing drugs (e.g., Latrunculin A, Cytochalasin D) would be necessary since the current data only shows the association/correlation. Was the block of AE by actin depolymerization observed?

Response R1.1: We agree with the reviewer but unfortunately, since actin polymerization and or depolymerization in the head are important for exocytosis, we cannot use this experimental approach to dissect both events. Addition of these inhibitors block the occurrence of AE (PMID: 12604633).

(2) Please provide the rationale for using FM4-64 to visualize the plasma membrane since it has been reported to selectively stain membranes of vacuolar organelles. What is the principle of increase of FM4-64 dye intensity, other than the correlation with midpiece contraction? For example, in lines 400-402: the authors mentioned that 'some acrosomereacted moving sperm within the perivitelline space had low FM4-64 fluorescence in the midpiece (Figure 6C). After 20 minutes, these sperm stopped moving and exhibited increased FM4-64 fluorescence, indicating midpiece contraction (Figure 6D).' While recognizing the increase of FM4-64 dye intensity can be an indicator of midpiece contraction, without knowing how and when the intensity of FM4-64 dye changes, it is hard to understand this observation. Please discuss.

Response R1.2: FM4-64 is an amphiphilic styryl fluorescent dye that preferentially binds to the phospholipid components of cell membranes, embedding itself in the lipid bilayer where it interacts with phospholipid head groups. Due to its amphiphilic nature, FM dyes primarily anchor to the outer leaflet of the bilayer, which restricts their internalization. It has been demonstrated that FM4-64 enters cells through endocytic pathways, making these dyes valuable tools for studying endocytosis.

Upon binding, FM4-64's fluorescence intensifies in a more hydrophobic environment that restricts molecular rotation, thus reducing non-radiative energy loss and enhancing fluorescence. These photophysical properties render FM dyes useful for observing membrane fusion events. When present in the extracellular medium, FM dyes rapidly reach a chemical equilibrium and label the plasma membrane in proportion to the availability of binding sites.

In wound healing studies, for instance, the fluorescence of FM4-64 is known to increase at the wound site. This increase is attributed to the repair mechanisms that promote the fusion of intracellular membranes at the site of the wound, leading to a rise in FM4-64 fluorescence. Similarly, an increase in FM4-64 fluorescence has been reported in the heads of both human and mouse sperm, coinciding with AE. In this scenario, the fusion between the plasma membrane and the acrosomal vesicle provides additional binding sites for FM4-64, thus increasing the total fluorescence observed in the head. This dynamic response of FM4-64 makes it an excellent marker for studying these cellular processes in real-time.

This study is the first to report an increase in FM4-64 fluorescence in the midpiece of the sperm flagellum. Figures 5 and Author response images 6 to 9 demonstrate that during the contraction of the sperm flagellum, structural rearrangements occur, including the compaction of the mitochondrial sheath and other membranous structures. Such contraction likely increases the local density of membrane lipids, thereby elevating the local concentration of FM4-64 and enhancing the probability of fluorescence emission. Additionally, changes in the microenvironment such as pH or ionic strength during contraction might further influence FM4-64’s fluorescence properties, as detailed by Smith et al. in the Journal of Membrane Biology (2010). The photophysical behavior of FM4-64, including changes in quantum yield due to tighter membrane packing or alterations in curvature or tension, may also contribute to the increased fluorescence observed. Notably, Figure S2 indicates that other fluorescent dyes like Memglow 700, Bodipy-GM, and FM1-43 also show a dramatic increase in their fluorescence during the midpiece contraction. Investigating whether the compaction of the plasma membrane or other mesoscale processes occur in the midpiece of the sperm flagellum could be a valuable area for future research. The use of fluorescent dyes such as LAURDAN or Nile Red might provide further insights into these membrane dynamics, offering a more comprehensive understanding of the biochemical and structural changes during sperm motility and gamete fusion events.

(3) As the volume of the whole midpiece stays the same while the diameter decreases along the whole midpiece (midpiece contraction), the authors need to describe what changes in the midpiece length they observe during the contraction. Was the length of the midpiece during the contraction measured and compared before and after contraction?

Response R1.3: As requested, we have measured the length of the midpiece in AI and AR sperm. As shown in Author response image 12 (For review purposes only), no statistically significant differences were observed. 

Author response image 12.

Midpiece length measured by the length of mitochondrial DsRed2 fluorescence in EGFP-DsRed2 sperm. Measurements were done before (acrosome-intact) and after (acrosome-reacted) acrosome exocytosis and midpiece contraction. Data is presented as the mean ± sem of 14 cells induced by 10 µM ionomycin. Paired t-test was performed, resulting in no statistical significance. 

(4) Most of all, it is not clear what the midpiece, thus mitochondria, contraction means in terms of sperm bioenergetics and motility cessation. Would the contraction induce mitochondrial depolarization or hyperpolarization, increase or decrease of ATP production/consumption? It will be great if this point is discussed. For example, an increase in mitochondrial Ca2+ is a good indicator of mitochondrial activity (ATP production).

Response R1.4: That is an excellent point. We have discussed this idea in the discussion (line 620-624). We are currently exploring this idea using different approaches because we also think that these changes in the midpiece may have an impact in the function of the mitochondria and perhaps, in their fate once they are incorporated in the egg after fertilization. 

(5) The authors claimed that Ca2+ signal propagates from head to tail, which is the opposite of the previous study (PMID: 17554080). Please clarify if it is a speculation. Otherwise, please support this claim with direct experimental evidence (e.g., high-speed calcium imaging of single cells).

Response R1.5: In that study, it was claimed that a [Ca2+]i  increase that propagates from the tail to the head occurs when CatSper is stimulated. They did not evaluate the occurrence of AE when monitoring calcium.

Our data is in agreement with our previous results (PMID: 26819478) that consistently indicated that only the[Ca2+]i  rise originating in the sperm head is able to promote AE. 

(6) Figure 4E: Please explain how come Fluo4 signal diameter can be smaller than FM4-64 dye if it stains plasma membrane (at 4' and 7').

Response R1.6: When colocalizing a diffraction-limited image (Fluo4) with a super-resolution image (FM4-64), discrepancies in signal sizes and locations can become apparent due to differences in resolution. The Fluo4 signal, being diffraction-limited, adheres to a resolution limit of approximately 200-300 nanometers under conventional light microscopy. This limitation causes the fluorescence signal to appear broader and less defined. Conversely, super-resolution microscopy techniques, such as SRRF (Super-Resolution Radial Fluctuations), achieve resolutions down to tens of nanometers, allowing FM4-64 to reveal finer details at the plasma membrane and display potentially smaller apparent sizes of stained structures. Although both dyes might localize to the same cellular regions, the higher resolution of the FM4-64 image allows it to show a more precise and smaller diameter of the midpiece of the flagellum compared to the broader, less defined signal of Fluo4. To address this, the legend of Figure 4E has been slightly modified to clarify that the FM4-64 image possesses greater resolution. 

(7) Figure 5D-G: the midpiece diameter of AR intact cells was shown ~ 0.8 um or more in Figure 2, while now the radius in Figure 5 is only 300 nm. Since the diameter of the whole midpiece is nearly uniform when the acrosome is intact, clarify how and what brings this difference and where the diameter/radius measurement is done in each figure.

Response R1.7: The difference resides in what is being measured. In Figure 2, the total diameter of the cell is measured, through the maximum peaks of FM4-64 fluorescence which is a probe against plasma membrane. As for Figure 5, the radius shown makes reference to the radius of the actin double helix within the midpiece. To that end, cells were fixed and stained with phalloidin, a F-actin probe.

Minor points

(8) Figure S1 title needs to be changed. The "Midpiece contraction" concept is not introduced when Figure S1 is referred to.

Response R1.8: This was corrected in the new version.

(9) Reference #19: the authors are duplicated.

Response R1.9: This was corrected in the new version.

(10) Line 315-318: sperm undergoing contraction -> sperm undergoing AR/AE?

Response R1.10: This was corrected in the new version.

(11) Line 3632 -> punctuation missing.

Response R1.11: Modified as requested.

(12) Movie S7: please add an arrow to indicate the spermatozoon of interest.

Response R1.12:  The arrow was added as suggested.

(13) Line 515: One result of this study was that the sperm flagellum folds back during fusion coincident with the decrease in the midpiece diameter. The authors did not provide an explanation for this observation. Please speculate the function of this folding for the fertilization process.

Response R1.13: As requested, this is now incorporated in the discussion. We speculate that the folding of the flagellum during fusion further facilitates sperm immobilization because it makes it more difficult for the flagellum to beat. Such processes can enhance stability and increase the probability of fusion success. Mechanistically, the folding may occur as a consequence of the deformation-induced stress that develops during the decrease of midpiece diameter. 

Reviewer #2 (Recommendations For The Authors):

(1) Figure 2C, D, E. Does "-1" on the X-axis mean one minute before induction? If so, the diameter is already smaller and FM4-64 fluorescence intensity is higher before the induction in the spontaneous group. Does the acrosome reaction already occur at "-1" in this group?

Response R2.1: Yes, “-1” means that the measurements of the diameter/FM4-64 fluorescence was done one minute before the induction. And it is correct that the diameter is smaller and FM464 fluorescence higher in the spontaneous group because these sperm underwent acrosome exocytosis before the induction, that is, spontaneously.

(2) Figure 3D. Purple dots are not shown in the graph on the right side.

Response R2.2: Modified as requested.

(3) Lines 404-406. "These results suggest that midpiece contraction and motility cessation occur only after acrosome-reacted sperm penetrate the zona pellucida". Since midpiece contraction and motility cessation also occur before the passage through the zona pellucida (Figure 9B), "only" should be deleted.

Response R2.3: Modified as requested.

Reviewer #3 (Recommendations For The Authors):

(1) Do the authors have a hypothesis as to why the observed decrease in midpiece parameter results in cessation of sperm motility? It would be beneficial for the manuscript to include a paragraph about potential mechanisms in the discussion.

Response R3.1: As requested, a potential mechanism has been proposed in the discussion section (line 644-656).

(2) Since the authors propose in Gervasi et al. 2018 that the actin helix might be responsible for the integrity of the mitochondrial sheath and the localization of the mitochondria, is it possible that the proposed change in plasma membrane diameter and actin helix remodeling for example alters the localization of the mitochondria? TEM should be able to reveal any associated structural changes. In its current state, the manuscript lacks experimental evidence supporting the author's claim that the "helical actin structure plays a role in the final stages of motility regulation". The authors should either include additional evidence supporting their hypothesis or tone down their conclusions in the introduction and discussion.

Response  R3.3: We agree with the reviewer. This is an excellent point. As suggested by this reviewer as well as the other reviewers, we have performed SEM to observe the changes in the midpiece observed after its contraction for two main reasons. First, to confirm this observation using a different approach that does not involve the use of membrane dyes. As shown in Author response image 6-10, we have observed that in addition to the midpiece diameter, there is a reorganization of the mitochondria sheet that is also suggested by the SIM experiments. These observations will be explored with more experiments to confirm the structural and functional changes that mitochondria undergo during the contraction. We are currently investigating this phenomenon, These results are now included in the new Figure  2F.

(3) In line 134: The authors write: 'Some of the acrosome reacted sperm moved normally, whereas the majority remained immotile". Do the authors mean that a proportion of the sperm was motile prior to acrosomal exocytosis and became immotile after, or were the sperm immotile to begin with? Please clarify.

Response R3.4: This statement is based on the quantification of the motile sperm after induction of AE within the AR population (Fig. 1C). 

(4) The authors do not provide any experimental evidence supporting the first scenario. In video 1 a lot of sperm do not seem to be moving to begin with, only a few sperm show clear beating in and out of the focal plane. The highlighted sperm that acrosome-reacted upon exposure to progesterone don't seem to be moving prior to the addition of progesterone. In contrast, the sperm that spontaneously acrosome react move the whole time. In video 1 this reviewer was not able to identify one sperm that stopped moving upon acrosomal exocytosis. Similarly in video 3, although the resolution of the video makes it difficult to distinguish motile from non-motile sperm. In video 2 the authors only show sperm that are already acrosome reacted. Please explain and provide additional evidence and statistical analysis supporting that sperm stop moving upon acrosomal exocytosis.

Response R3.5: In videos 1 and 3, the cells are attached to the glass with concanavalin-A, this lectin makes sperm immotile (if well attached) because both the head and tail stick to the glass. The observed motility of sperm in these videos is likely due to them not being properly attached to the glass, which is completely normal. On the contrary, in videos 2 and 4, sperm are attached to the glass with laminin. This is a glycoprotein that only binds the sperm to the glass through its head, that is why they move freely.

(5) Could the authors provide additional information about the FM4-64 fluorescent dye?

What is the mechanism, and how does it visualize structural changes at the flagellum? Since the whole head lights up, does that mean that the dye is internalized and now stains additional membranes, similar to during wound healing assays (PMID 20442251, 33667528). Or is that an imaging artifact? How do the authors explain the correlation between FM4-64 fluorescence increase in the midpiece and the observed change in diameter? Does FM4-64 have solvatochromatic properties?

Response R3.6: We appreciate the insightful queries posed by Reviewer 3, which echo the concerns initially brought forward by Reviewer 1. For a detailed explanation of the mechanism of FM4-64 dye, how we interpret  it, visualizes structural changes in the flagellum, and its behavior during cellular processes, please refer to our detailed response in Response R1.2. In brief, FM464 is a lipophilic styryl dye that preferentially binds to the outer leaflets of cellular membranes due to its amphiphilic nature. Upon binding, the dye becomes fluorescent, allowing for the visualization of membrane dynamics. The increase in fluorescence in the sperm head or midpiece likely results from the dye’s accumulation in areas where membrane restructuring occurs, such as during AE or in response to changes in the flagellum structure.

Regarding the specific questions about internalization and whether FM4-64 stains additional membranes similarly to what is observed in wound healing assays, it's important to note that FM4-64 can indeed be internalized through endocytosis and subsequently label internal vesicular structures. Additionally, FM4-64 may experience changes in its fluorescence as a result of fusion events that increase the lipid content of the plasma membrane, as observed in studies cited (PMID 20442251, 33667528). This characteristic makes FM4-64 valuable not only for outlining cell membranes but also for tracking the dynamics of both internal and external membrane systems, particularly during cellular events that involve significant membrane remodeling, such as wound healing or AE.

Concerning whether the increased fluorescence and observed changes in diameter are artifacts or reflect real biological processes, the correlation observed likely indicates actual changes in the midpiece architecture through molecular mechanisms that remain to be further elucidated. The data presented in Figures 5 and Author response images 6-10 support that this increase in fluorescence is not merely an artifact but a feature of how FM4-64 interacts with its environment. 

Finally, regarding the solvatochromatic properties of FM4-64, while the dye does show changes in its fluorescence intensity in different environments, its solvatochromatic properties are generally less pronounced than those of dyes specifically designed to be solvatochromatic. FM464's fluorescence changes are more a result of membrane interaction dynamics and dye concentration than of solvatochromatic shifts. 

(6) For the experiment summarized in Figure S1, did the authors detect sperm that acrosome-reacted upon exposure to progesterone and kept moving? This reviewer is wondering how the authors reliably measure FM4-64 fluorescence if the flagellum moves in and out of the focal plane. If the authors observe sperm that keep moving, what was the percentage within a sperm population and how did FM4-64 fluorescence change?

Response R3.6: We did identify sperm that underwent acrosome reaction upon exposure to progesterone and continued to exhibit movement. However, due to the issue raised by the reviewer regarding the flagellum going out of focus, we opted to quantify the percentage of sperm that were adhered to the slide (using laminin). This approach allows for the observation of flagellar position over time, facilitating an easy assessment of fluorescence changes. The percentage of sperm that maintained movement after AE is depicted in Figure 1C.

(7) In Figure S1B it doesn't look like the same sperm is shown in all channels or time points, the hook shown in the EGFP channel is not always pointing in the same direction. If FM4-64 is staining the plasma membrane, how do the authors explain that the flagellum seems to be more narrow in the FM4-64 channel than in the brightfield and DsRed2 channel?

Response 3.7: It is the same sperm, but due to technical limitations images were sequentially acquired. For example, for time 5 minutes after progesterone, all images in DIC were taken, then all images in the EGFP channel, then DsRed2* and finally FM4-64. The reason for this was to acquire images as fast as possible, particularly in DIC images which were then processed to get the beat frequency.

Regarding the flagellum that seems to be more narrow in the FM4-64 channel compared to the BF or DsRed2 channel, the explanation is related to the fact that intensity of the DsRed2 signal is stronger than the other two. This higher signal may have increased the amount of photons captured by the detector.

(8) Overall, it would be beneficial to include statistics on how many sperm within a population did change FM4-64 fluorescence during AE and how many did not, in addition to information about motility changes and viability. Did the authors exclude that the addition of FM4-64 causes cell death which could result in immotile sperm or that only dying sperm show an increase in FM4-64 fluorescence?

Response 3.8: The relationship between cell death and the increase in FM4-64 fluorescence is widely discussed in Response P2.3. In our experiments, we always considered sperm that were motile to hypothesize about the relevance of this observation. We have two types of experiments: 

(1) Sperm-egg Fusion: In experiments where sperm and eggs were imaged to observe their fusion, sperm were initially moving and after fusion, the midpiece contraction (increase in FM4-64 fluorescence was observed) indicating that the change in the midpiece (that was observed consistently in all fusing cells analyzed), is part of the process. 

(2) Sperm that underwent AE: we have observed two behaviours as shown in Figure 1: 

a) Sperm that underwent AE and they remain motile without midpiece contraction (they are alive for sure); 

b) Sperm that underwent AE and stopped moving with an increase in FM464 fluorescence. We propose that this contraction during AE is not desired because it will impede sperm from moving forward to the fertilization site when they are in the female reproductive tract. In this case, we acknowledge that the cessation of sperm motility may be attributed to cellular death, potentially correlating with the increased FM4-64 signal observed in the midpiece of immotile sperm that have undergone AE. To address this hypothesis, we conducted image-based flow cytometry experiments, which are well-suited for assessing cellular heterogeneity within large populations.

Regarding the relationship between the increase in FM4-64 and AE, we have always observed that AE is followed by an increase in FM4-64 in the head in mice (PMID: 26819478) as well as in human (PMID: 25100708) sperm. This was originally corroborated with the EGFP sperm. However, not all the cells that undergo AE increase the FM4-64 fluorescence in the midpiece.

(9) The authors report that a fraction of sperm undergoes AE without a change in FM4-64 fluorescence (Figure 1F). How does the [Ca2+]i change in those cells? Again statistics on the distribution of a certain pattern within a population in addition to showing individual examples would be very helpful.

Response 3.9: A recent work shows that an initial increase in [Ca2+]i  is required to induce changes in flagellar beating necessary for hyperactivation (Sánchez-Cárdenas et al., 2018). However, when [Ca2+]i  increases beyond a certain threshold, flagellar motility ceases. These conclusions are based on single-cell experiments in murine sperm with different concentrations of the Ca2+ ionophore, A23187. The authors reported that complete loss of motility was observed when using ionophore concentrations higher than 1 μM. In contrast, spermatozoa incubated with 0.5 μM A23187 remained motile throughout the experiment. Once the Ca2+ ionophore is removed, the sperm would reduce the concentration of this ion to levels compatible with motility and hyperactivation (Navarrete et al., 2016). However, some of the washed cells did not recover mobility in the recorded time window (Sánchez-Cárdenas et al., 2018). These results would indicate that due to the increase in [Ca2+]i  induced by the ionophore, irreversible changes occurred in the sperm flagellum that prevented recovery of mobility, even when the ionophore was not present in the recording medium. 

Taking into account our results, one possible scenario to explain this irreversible change would be the contraction of the midpiece. Our results demonstrate that the increase in [Ca2+]i observed in the midpiece (whether by induction with progesterone, ionomycin or occurring spontaneously) causes the contraction of this section of the flagellum and its subsequent immobilization. 

(10) While the authors results show that changes in [Ca2+]i correlate with the observed reduction of the midpiece diameter, they do not provide evidence that the structural changes are triggered by Ca2+i influx. It could just be a coincidence that both events spatially overlap and that they temporarily follow each other. The authors should either provide additional evidence or tone down their conclusion.

Response 3.10: We agree with the reviewer. As suggested, we have toned down our conclusion.

(11) Are the authors able to detect the changes in the midpiece diameter independent from FM4-64 or other plasma membrane dyes? An alternative explanation could be that the dyes are internalized due to cell death and instead of staining the plasma membrane they are now staining intracellular membranes, resulting in increased fluorescence and giving the illusion that the midpiece diameter decreased. How do the authors explain that the Bodipy-GM1 Signal directly overlaps with DsRed2 and SIR-actin, shouldn't there be some gap? Since the rest of the manuscript is based on that proposed decrease in midpiece diameter the authors should perform orthogonal experiments to confirm their observation.

Response 3.11: As requested by the reviewer, we have not used new methods to visualize the change in sperm diameter in the midpiece. In neither of them, a membrane dye was used. First, we have performed immunofluorescence to detect a membrane protein (GLUT3). Second, we have used scanning electron microscopy. The results are now incorporated in the new Figure 2FG. In both experiments, a change in the midpiece diameter was observed. Please, also visit responses P2.5 and Author response images 8 to 10.  

Regarding the overlap between the signal of Bodipy GM1 (membrane) and the fluorescence of DsRed2 (mitochondria) and Sir-Actin (F-actin), it is only observed in acrosomereacted sperm, not in acrosome-intact sperm (Figure S4). In our view, these structures become closed after midpiece contraction, and the resolution of the images is insufficient to distinguish them clearly. This issue is also evident in Figure 5B. Therefore, we conducted additional experiments using more powerful super-resolution techniques such as STORM (Figures 5D-F).

(12) The proposed gap of 200 nM between the actin helix and the plasma membrane, has been observed by TEM? Considering that the diameter of the mouse sperm midpiece is about 1 um, that is a lot of empty space which leaves only about 600 nm for the rest of the flagellum. The axoneme is 300 nm and there needs to be room for the ODFs and the mitochondria. Please explain.

Response 3.12: Unfortunately, the filament of polymerized actin cannot be observed by TEM. Furthermore, we were discouraged from trying other approaches, such as utilizing phalloidin gold, because for some reason, it does not work properly.

In our view, the 200 nm gap between the actin cytoskeleton and the plasma membrane is occupied by the mitochondria (that is the size that it is frequently reported based on TEM; see https://doi.org/10.1172/jci.insight.166869).

(13) The results provided by the authors do not convince this reviewer that the actin helix moves, either closer to the plasma membrane or toward the mitochondria, the observed differences are minor and not confirmed by statistical analysis.

Response 3.13: As requested, the title of that section was changed. Moreover, our conclusion is exactly as the reviewer is suggesting: “Since the results of the analysis of SiR-actin slopes were not conclusive, we studied the actin cytoskeleton structure in more detail”. This conclusion is based on the statistical analysis shown in Figure S5D-E.

(14) The fluorescence intensity of all plasma membrane dyes increases in all cells chosen by the authors for further analysis. Could the increase in SiR-Actin fluorescence be explained by a microscopy artifact instead of actin helix remodeling? Alternatively, can the authors exclude that the observed increase in SIR-Actin might be an artifact caused by the increase in FM4-64 fluorescence? Since the brightness in the head similarly increases to the fluorescence in the flagellum the staining pattern looks suspiciously similar. Did the authors perform single-stain controls?

Response 3.14: We had similar concerns when we were doing the experiments using SiR-actin. Although we have performed single stain controls to make sure that the actin helix remodelling occurs during the midpiece contraction, we have performed experiments using higher resolution techniques such as STORM using a different probe to stain actin (Phalloidin).

(15) Should actin cytoskeleton remodeling indeed result in a decrease of actin helix diameter, what do the authors propose is the underlying mechanism? Shouldn't that result in changes in mitochondrial structure or location and be visible by TEM? This reviewer is also wondering why the authors focus so much on the actin helix, while the plasma membrane based on the author's results is moving way more dramatically.

Response 3.15: This raises an intriguing point. Currently, we lack an understanding of the underlying mechanism driving actin remodeling, and we are eager to conduct further experiments to explore this aspect. For instance, we are investigating the potential role of Cofilin in remodeling the F-actin network. Initial experiments utilizing STORM imaging have revealed the localization of Cofilin in the midpiece region, where the actin helix is situated.

Regarding mitochondria, thus far, we have not uncovered any evidence suggesting that acrosome reaction or fusion with the egg induces a rearrangement of these organelles within the structure. The rationale for investigating polymerized actin in depth stems from the fact that, alongside the axoneme and other flagellar structures such as the outer dense fibers and fibrous sheet, these are the sole cytoskeletal components present in that particular tail region.

(14) The fact that the authors observe that most sperm passing through the zona pellucida, which requires motility, display high FM4-64 fluorescence, doesn't that contradict the authors' hypothesis that midpiece contraction and motility cessation are connected? Videos confirming sperm motility and information about pattern distribution within the observed sperm population in the perivitelline space should be provided.

Response 3.14: We believe it is a matter of time, as depicted in Figure 1D, our model shows that first the cells lose the acrosome, present motility and low FM4-64 fluorescence in the midpiece (pattern II) and after that, they lose motility and increase FM4-64 fluorescence in the midpiece (pattern III). That is why, we think that when sperm pass the zona pellucida they present pattern II and after some time they evolve into pattern III. 

(15) In the experiments summarized in Figure 8, did all sperm stop moving? Considering that 74 % of the observed sperm did not display midpiece contraction upon fusion, again doesn't that contradict the authors' hypothesis that the two events are interdependent? Similarly, in earlier experiments, not all acrosome-reacted sperm display a decrease in midpiece diameter or stop moving, questioning the significance of the event. If some sperm display a decrease in midpiece diameter and some don't, or undergo that change earlier or later, what is the underlying mechanism of regulation? The observed events could similarly be explained by sperm death: Sperm are dying × plasma membrane integrity changes and plasma membrane dyes get internalized × [Ca2+]i simultaneously increases due to cell death × sperm stop moving.

Response 3.15: The percentage of sperm that did not exhibit midpiece contraction in Fig.8B is 26%, not 74%, indicating that it does not contradict our hypothesis. However, this still represents a significant portion of sperm that remain unchanged in the midpiece, leaving room for various explanations. For instance, it's possible that: i) the change in fluorescence was not detected due to the event occurring after the recording concluded, or ii) in some instances, this alteration simply does not occur. Nevertheless, we did not track subsequent events in the oocyte, such as egg activation, to definitively ascertain the success of fusion. Incorporation of the dye only manifests the initiation of the process.

(16) The authors propose changes in Ca2+ as one potential mechanism to regulate midpiece contraction, however, the Ca2+ measurements during fusion are flawed, as the authors write in the discussion, by potential Ca2+ fluorophore dilution. Considering that the authors observe high Ca2+ in all sperm prior to fusion, could that be a measuring artifact? Were acrosome-intact sperm imaged with the same settings to confirm that sperm with low and high Ca2+ can be distinguished? Should [Ca2+]i changes indeed be involved in the regulation of motility cessation during fusion, could the authors speculate on how [Ca2+]i changes can simultaneously be involved in the regulation of sperm hyperactivation?

Response 3.16: We agree with the reviewer that our experiments using calcium probes are not conclusive for many technical problems. We have toned down our conclusions in the new version of the manuscript.

(17) 74: AE takes place for most cells in the upper segment of the oviduct, not all of them.

Please correct.

Response 3.17: Corrected in the new version.

(18) 88: Achieved through, or achieved by, please correct.

Response 3.18: Corrected in the new version.

(19) 243: Acrosomal exocytosis initiation by progesterone, please specify.

Response 3.19: Modified in the new version.

(20) 277: "The actin cytoskeleton approaches the plasma membrane during the contraction of the midpiece" is misleading. The author's results show the opposite.

Response 3.20: As suggested, this statement was modified.

(21) 298: Why do the authors find it surprising that the F-actin network was unchanged in acrosome-intact sperm that do not present a change in midpiece diameter?

Response 3.21: The reviewer is right. The sentence was modified.

(22) Figures 5D,F: The provided images do not support a shift in the actin helix diameter.

Response 3.22: The shift in the actin helix diameter is provided in Figure 5E and 5G.

(23) Figure S5C: The authors should show representative histograms of spontaneously-, progesterone induced-, and ionomycin-induced AE. Based on the quantification the SiRactin peaks don't seem to move when the AR is induced by progesterone.

Response 3.23: As requested, an ionomycin induced sperm is incorporated.

(24) 392: Which experimental evidence supports that statement?

Response 3.24: A reference was incorporated. 

Reference 13 is published, please update. Response 3.25: updated as requested.

eLife assessment

This important work substantially advances our understanding of sperm motility regulation during fertilization process by uncovering the midpiece/mitochondria contraction associated with motility cessation and structural changes in the midpiece actin network as its mode of action involved. The evidence supporting the conclusion is solid, with rigorous live cell imaging using state-of-art microscopy, although more functional analysis of the midpiece/mitochondria contraction would have further strengthened the study. The work will be of broad interest to cell biologists working on the cytoskeleton, mitochondria, cell fusion, and fertilization.

Reviewer #2 (Public Review):

Summary:

The authors used state-of-the-art microscopy to analyze the structural changes that occur in sperm tails after the acrosome reaction. They found that midpiece contraction and actin reorganization occurred, which is associated with the cessation of flagellar motility during sperm-egg fusion. The mechanism by which flagellar motility is arrested during sperm-oocyte fusion is unknown, and this study proposes its novel mechanism and provides important insights for cell and reproductive biologists.

In the revised manuscript, the authors addressed most of my concerns.

Strength:

Various microscopy techniques including super-resolution microscopy and scanning electron microscopy were used to analyze structural organization of the midpiece in detail.

Reviewer #3 (Public Review):

While progressive and also hyperactivated motility are required for sperm to reach the site of fertilization and to penetrate oocyte's outer vestments, during fusion with the oocyte's plasma membrane it has been observed that sperm motility ceases. Identifying the underlying molecular mechanisms would provide novel insights into a crucial but mostly overlooked physiological change during the sperm's life cycle. In this publication the authors aim to provide evidence that the helical actin structure surrounding the sperm mitochondria in the midpiece plays a role in regulating sperm motility, specifically the motility arrest during sperm fusion but also during earlier cessation of motility in a subpopulation of sperm post acrosomal exocytosis.

The main observation the authors make is that in a subpopulation of sperm undergoing acrosomal exocytosis and sperm that fuse with the plasma membrane of the oocyte display a decrease in midpiece parameter of 30 nm. The authors propose the decrease in midpiece diameter via various microscopy techniques based on membrane dyes and bright-field images. In the revised version of the manuscript, a change in midpiece diameter is now confirmed via electron microscopy, even though the difference is not significant. The authors also propose that the midpiece diameter decrease is driven by changes in sperm intracellular Ca2+ and structural changes of the actin helix network. Future studies are still needed to confirm the casualty of these events and explore the discrepancy between fluorescence microscopy results and SEM. Overall, the authors should further tone down their conclusions.

eLife assessment

This important study combines prospective cohort, metabolomics and machine learning to identify a panel of nine circulating metabolites that improved the ability in risk prediction of progression from prediabetes to diabetes. The findings are convincing, and using current state-of-the-art methods the data and analyses support the claims. This paper provides insights into the integration of these metabolites into clinical and public health practice.

Reviewer #1 (Public review):

Using the UK Biobank, this study assessed the value of nuclear magnetic resonance measured metabolites as predictors of progression to diabetes. The authors identified a panel of 9 circulating metabolites that improved the ability in risk prediction of progression from prediabetes to diabetes. In general, this is a well-performed study, and the findings may provide a new approach to identifying those at high risk of developing diabetes.

Comments on the revised version:

Thanks so much for carefully addressing my comments.

Reviewer #2 (Public review):

Deciphering the metabolic alterations characterizing the prediabetes-diabetes spectrum could provide early time windows for targeted preventive measures to extend precision medicine while avoiding disproportionate healthcare costs. The authors identified a panel of 9 circulating metabolites combined with basic clinical variables that significantly improved the prediction from prediabetes to diabetes. These findings provided insights into the integration of these metabolites into clinical and public health practice.

Comments on the revised version:

Congratulations to the authors. I have no more comments.

Author response:

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

Reviewer #1 (Public Review):

Using the UK Biobank, this study assessed the value of nuclear magnetic resonance measured metabolites as predictors of progression to diabetes. The authors identified a panel of 9 circulating metabolites that improved the ability in risk prediction of progression from prediabetes to diabetes. In general, this is a well-performed study, and the findings may provide a new approach to identifying those at high risk of developing diabetes. I have some comments that may improve the importance of this study.

We deeply appreciate the reviewer's invaluable time dedicated to the review of this manuscript and the insightful comments to enhance its overall quality.

(1) It is unclear why the authors only considered the top 20 variables in the metabolite selection and why they did not set a wider threshold.

Thank you for the comment. We set the top 20 variables in the metabolite selection balancing the performance of the final diabetes risk prediction model and the clinical applicability due to measurement costs. We have added this explanation in the “Methods” section.

“We chose the intersection set of the top 20 most important variables selected by the three machine learning models, after balancing the performance of the final diabetes risk prediction model and the clinical applicability associated with measurement costs of metabolites.”

(2) The methods section would benefit from a more detailed exposition of how parameter tuning was conducted and the range of parameters explored during the training of the RSF model.

According to the reviewer’s suggestion, we have added a more detailed description of parameters tunning and the range of parameters explored during the training of the RSF model in the “Method S3” section in the Supplementary material.

“The RSF model was fitted using the “randomForestSRC” package and the grid search method was used for hyperparameter tuning. Specifically, the grid search method was used to tune hyperparameters among the RSF model, through minimizing out-of-sample or out-of-bag error1. Each tree in the RSF is constructed from a random sample of the data, typically a bootstrap sample or 63.2% of the sample size (as in the present study). Consequently, not all observations are used to construct each tree. The observations that are not used in the construction of a tree are referred to as out-of-bag observations. In an RSF model, each tree is built from a different sample of the original data, so each observation is “out-of-bag” for some of the trees. The prediction for an observation can then be obtained using only those trees for which the observation was not used for the construction. A classification for each observation is obtained in this way and the error rate can be estimated from these predictions. The resulting error rate is referred to as the out-of-bag error. Through calculating the out-of-bag error in each iteration, the best hyperparameters were finally determined.

The hyperparameters to be tuned and range of grid search in the present study were below: number of trees (50-1000, by 50), number of variables to possibly split at each node (3-6, by 1), and minimum size of terminal node (1-20, by 1)2.”

(3) It is hard to understand the meaning of the decision curve analysis and the clinical implications behind the net benefit, which are required to clarify the application values of models.

Thank you for the comment. We have added more description and discussion about the decision curve analysis in the “Methods” and “Discussion” sections.

“Furthermore, we used decision curve analysis (DCA) to assess the clinical usefulness of prediction model-based guidance for prediabetes management, which calculates a clinical “net benefit” for one or more prediction models in comparison to default strategies of treating all or no patients3.”

“Most importantly, a model with good discrimination does not necessarily have high clinical value. Hence, DCA was used to compare the clinical utility of the model before and after adding the metabolites, and this showed a higher net benefit for the latter than the basic model, suggesting the addition of the metabolites increased the clinical value of prediction, i.e., the potential benefit of guiding management in individuals with prediabetes3,4. These results provided novel evidence supporting the value of metabolic biomarkers in risk prediction and stratification for the progression from prediabetes to diabetes.”

(4) Notably, the NMR platform utilized within the UK Biobank primarily focused on lipid species. This limitation should be discussed in the manuscript to provide context for interpreting the results and acknowledge the potential bias from the measuring platform.

Thank you for the comment. We acknowledged this limitation that NMR platform within the UK Biobank primarily focused on lipid species and the potential bias from the measuring platform and have added this in “Discussion” section.

“Third, the Nightingale metabolomics platform primarily focused on lipids and lipoprotein sub-fractions, and thus the predictive value of other metabolites in the progression from prediabetes to diabetes warranted further research using an untargeted metabolomics approach.”

(5) The manuscript should explain the potential influence of non-fasting status on the findings, particularly concerning lipoprotein particles and composition. There should be a detailed discussion of how non-fasting status may impact the measurement and the findings.

According to the reviewer’s suggestion, we have added more details to explain the potential influence of non-fasting status on our findings in the “Discussion” section.

“Additionally, the use of non-fasting blood samples might increase inter-individual variation in metabolic biomarker concentrations, however, fasting duration has been reported to account for only a small proportion of variation in plasma metabolic biomarker concentrations5. Therefore, we believe the impact of non-fasting samples on our findings would be minor.”

(6) Cross-platform standardization is an issue in metabolism, and further descriptions of quality control are recommended.

Thank you for the comment. We have added more description of quality control in the “Method S1” section in the Supplementary material.

“Metabolic biomarker profiling by Nightingale Health’s NMR platform provides consistent results over time and across spectrometers. Furthermore, the sample preparation is minimal in the Nightingale Health’s metabolic biomarker platform, circumventing all extraction steps. These aspects result in highly repeatable biomarker measurements. Pre-specified quality metrics were agreed between UK Biobank and Nightingale Health to ensure consistent results across the samples, and pilot measurements were conducted. Nightingale Health performed real-time monitoring of the measurement consistency within and between spectrometers throughout the UK Biobank samples. Two control samples provided by Nightingale Health were included in each 96-well plate for tracking the consistency across multiple spectrometers. Furthermore, two blind duplicate samples provided by the UK Biobank were included in each well plate, with the position information unlocked only after results delivery. Coefficient of variation (CV) targets across the metabolic biomarker profile were pre-specified for both Nightingale Health’s internal control samples and UK Biobank’s blind duplicates. The targets were met for each consecutively measured batch of ~25,000 samples. For the majority of the metabolic biomarkers, the CVs were below 5% (https://biobank.ndph.ox.ac.uk/showcase/refer.cgi?id=3000). Further, the distributions of measured biomarkers from 5 sample batches indicated absence of batch effects (https://biobank.ctsu.ox.ac.uk/ukb/ukb/docs/nmrm_app1).”

Reviewer #2 (Public Review):<br /> Deciphering the metabolic alterations characterizing the prediabetes-diabetes spectrum could provide early time windows for targeted preventive measures to extend precision medicine while avoiding disproportionate healthcare costs. The authors identified a panel of 9 circulating metabolites combined with basic clinical variables that significantly improved the prediction from prediabetes to diabetes. These findings provided insights into the integration of these metabolites into clinical and public health practice. However, the interpretation of these findings should take account of the following limitations.

We appreciate the reviewer’s positive comments and encouragement.

(1) First, the causal relationship between identified metabolites and diabetes or prediabetes deserves to be further examined particularly when the prediabetic status was partially defined. Some metabolites might be the results of prediabetes rather than the casual factors for progression to diabetes.

Thank you for your insightful comments. We agree with you that the panel of metabolites in this study might not be the causal factor for progression from prediabetes to diabetes, which needs further validation in experimental studies. We have added this limitation in the “Discussion” section.

“Fifth, we could not draw any conclusion about the causality between the identified metabolites and the risk for progression to diabetes due to the observational nature, which remained to be validated in further experimental studies.”

(2) The blood samples were taken at random (not all in a non-fasting state) and so the findings were subjected to greater variability. This should be discussed in the limitations.

According to the reviewer’s suggestion, we have added more details to explain the potential influence of non-fasting status on our findings in the “Discussion” section.

“Additionally, the use of non-fasting blood samples might increase inter-individual variation in metabolic biomarker concentrations, however, fasting duration has been reported to account for only a small proportion of variation in plasma metabolic biomarker concentrations5. Therefore, we believe the impact of non-fasting samples on our findings would be minor.”

(3) The strength of NMR in metabolic profiling compared to other techniques (i.e., mass spectrometry [MS], another commonly used metabolic profiling method) could be added in the Discussion section.

According to the reviewer’s suggestion, we have added the strength of NMR in metabolic profiling compared to other techniques in the “Discussion” section.

“Circulating metabolites were quantified via NMR-based metabolome profiling within the UK Biobank, which offers metabolite qualification with relatively lower costs and better reproducibility6.”

(4) Fourth, the applied platform focuses mostly on lipid species which may be a limitation as well.

Thank you for the comment. We acknowledged this limitation that NMR platform within the UK Biobank primarily focused on lipid species and the potential bias from the measuring platform and have added this in the “Discussion” section.

“Third, the Nightingale metabolomics platform primarily focused on lipids and lipoprotein sub-fractions, and thus the predictive value of other metabolites in the progression from prediabetes to diabetes warranted further research using an untargeted metabolomics approach.”

(5) It is a very large group with pre-diabetes, but the results only apply to prediabetes and not to the general population. This should be clear, although the authors have also validated the predictive value of these metabolites in the general population.

Thank you for the comment. We agree with you that the results only apply to prediabetes and not to the general population, though they also showed potential predictive value among participants with normoglycemia. We have accordingly modified the relevant expressions in the “Conclusion” section to restrict these findings to participants with prediabetes.

“In this large prospective study among individuals with prediabetes, we detected a panel of circulating metabolites that were associated with an increased risk of progressing to diabetes.”

Recommendations for the Authors:

Thank you for providing the valuable feedback and the time you have dedicated to our work.

(1) In the first paragraph of the Discussion section, please include the specific names of the metabolites selected from machine learning methods.

Thank you for your comment and we have added accordingly in the first paragraph of the “Discussion” section.

“More importantly, our findings suggested that adding the selected metabolites (i.e., cholesteryl esters in large HDL, cholesteryl esters in medium VLDL, triglycerides in very large VLDL, average diameter for LDL particles, triglycerides in IDL, glycine, tyrosine, glucose, and docosahexaenoic acid) could significantly improve the risk prediction of progression from prediabetes to diabetes beyond the conventional clinical variables.”

(2) To enhance the readability and simplicity of the paper, the description of covariate collection in the methods section should be streamlined, with detailed information provided in the supplementary materials.

Thank you for your suggestion and we have moved details about covariates collection to the “Supplementary method S2” to enhance the readability and simplicity of the paper.

“Information on covariates was collected through a self-completed touchscreen questionnaire or verbal interview at baseline, including age, sex, ethnicity, Townsend deprivation index, household income, education, employment status, smoking status, moderate alcohol, physical activity, healthy diet score, healthy sleep score, family history of diabetes, history of cardiovascular disease (CVD), history of hypertension, history of dyslipidemia, history of chronic lung diseases (CLD), and history of cancer.

Physical measurements included systolic (SBP) and diastolic blood pressure (DBP), height, weight, waist circumference (WC), and hip circumference (HC). Body mass index (BMI) was calculated as weight in kilograms divided by the square of height in meters (kg/m²). Missing covariates were imputed by the median value for continuous variables and a missing indicator for categorical variables. More details about covariates collection can be found in Method S2.”

3. Title for Table 2, using Cox proportional hazards prediction models is not common. You may consider the title "Performance of Cox proportional hazards regression models in prediction of progression of prediabetes to diabetes".

Thank you for your suggestion and we have revised it accordingly.

4. Figure 3, did the authors consider competing risk to compute cumulative incidence function?

Thank you for your comment. We did not consider competing risk from death when plotting the cumulative hazard curves. However, following your suggestion, we have included an additional cumulative hazard plot after considering the competing

References

(1) Janitza S, Hornung R. On the overestimation of random forest's out-of-bag error. PLoS One. 2018;13(8):e0201904.

(2) Tian D, Yan HJ, Huang H, et al. Machine Learning-Based Prognostic Model for Patients After Lung Transplantation. JAMA Netw Open. 2023;6(5):e2312022.

(3) Vickers AJ, van Calster B, Steyerberg EW. A simple, step-by-step guide to interpreting decision curve analysis. Diagn Progn Res. 2019;3:18.

(4) Li J, Xi F, Yu W, Sun C, Wang X. Real-Time Prediction of Sepsis in Critical Trauma Patients: Machine Learning-Based Modeling Study. JMIR Form Res. 2023;7:e42452.

(5) Li-Gao R, Hughes DA, le Cessie S, et al. Assessment of reproducibility and biological variability of fasting and postprandial plasma metabolite concentrations using 1H NMR spectroscopy. PLoS One. 2019;14(6):e0218549.

(6) Geng T-T, Chen J-X, Lu Q, et al. Nuclear Magnetic Resonance–Based Metabolomics and Risk of CKD. American Journal of Kidney Diseases. 2023.

eLife assessment

This important study adopts a comprehensive approach: functional connectivity, biochemistry, and psychophysics to reveal a holistic understanding of the relationship between GABA-ergic inhibition in the human MT+ region and visuo-spatial intelligence. The evidence supporting the conclusion is convincing. The result advances our understanding of how the human MT+ is assemble into complex cognition as an intellectual hub, and will be of interest to researchers in psychology, cognitive science, and neuroscience.

Reviewer #1 (Public review):

Summary:

The study of human intelligence has been the focus of cognitive neuroscience research, and finding some objective behavioral or neural indicators of intelligence has been an ongoing problem for scientists for many years. Melnick et al, 2013 found for the first time that the phenomenon of spatial suppression in motion perception predicts an individual's IQ score. This is because IQ is likely associated with the ability to suppress irrelevant information. In this study, a high-resolution MRS approach was used to test this theory. In this paper, the phenomenon of spatial suppression in motion perception was found to be correlated with the visuo-spatial subtest of gF, while both variables were also correlated with the GABA concentration of MT+ in the human brain. In addition, there was no significant relationship with the excitatory transmitter Glu. At the same time, SI was also associated with MT+ and several frontal cortex FCs.

Strengths:

(1) 7T high-resolution MRS is used<br /> (2) This study combines the behavioral tests, MRS, and fMRI.

Major<br /> I have no further comments. The approach and experiment are sound. The only overall drawback is the relatively low sample size.

Weaknesses:<br /> (1) Line 138, "This finding supports the hypothesis that motion perception is associated with neural activity in MT+ area". This sentence is strange because it is a well-established finding in numerous human fMRI papers. I think the authors should be more specific about what this finding implies.

Response: We thank reviewer for pointing this out. We have revised it to:" This finding is in line with prior results, which indicates that motion perception is associated with neural activity in hMT+ area, but not in EVC (primarily in V1)" (lines 156-158)

Reply: This argument should be refined. Numerous studies have shown the key role of V1 in motion perception. V1 contains a vast proportion of direction selective neurons. I am asking how your results here are related to existing literature. This argument is incorrect and too rough. Can you please revise this?

(9) Line 213, as far as I know, the study (Melnick et al., 2013) is a psychophysical study and did not provide evidence that the spatial suppression effect is associated with MT+.

Response: We thank reviewer for pointing this out. It was a mistake to use this reference, and we have revised it accordingly. (line 242)

Reply: Thanks. New citation is good. But that paper is a modeling study. The direct empirical evidence on humans should be as follow:

Tadin, D., Silvanto, J., Pascual-Leone, A. & Battelli, L. (2011) Improved motion perception and impaired spatial suppression following disruption of cortical area MT/V5. Journal of Neuroscience, 31, 1279-1283.

Reviewer #3 (Public review):

Summary:

This study aims to understand the role of GABA-ergic inhibition in the human MT+ region in predicting visuo-spatial intelligence through a combination of behavioral measures, fMRI (for functional connectivity measurement), and MRS (for GABA/glutamate concentration measurement). It provides useful evidence that GABA levels in the sensory cortex, such as in the human MT+, are associated with visuo-spatial ability, thus highlighting the importance of GABA-ergic inhibition in complex cognition.

Strengths:

(1) Comprehensive Approach: The study adopts a multi-level approach, i.e., neurochemical analysis of GABA levels, functional connectivity, and behavioral measures to provide a holistic understanding of the relationship between GABA-ergic inhibition and visuo-spatial intelligence.<br /> (2) Sophisticated Techniques: The use of ultra-high field magnetic resonance spectroscopy (MRS) technology for measuring GABA and glutamate concentrations in the MT+ region is a recent development.

Weaknesses:

The authors have carefully addressed the major weaknesses previously mentioned.

Author response:

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

Reviewer #1 (Public Review):

Summary:

The study of human intelligence has been the focus of cognitive neuroscience research, and finding some objective behavioral or neural indicators of intelligence has been an ongoing problem for scientists for many years. Melnick et al, 2013 found for the first time that the phenomenon of spatial suppression in motion perception predicts an individual's IQ score. This is because IQ is likely associated with the ability to suppress irrelevant information. In this study, a high-resolution MRS approach was used to test this theory. In this paper, the phenomenon of spatial suppression in motion perception was found to be correlated with the visuo-spatial subtest of gF, while both variables were also correlated with the GABA concentration of MT+ in the human brain. In addition, there was no significant relationship with the excitatory transmitter Glu. At the same time, SI was also associated with MT+ and several frontal cortex FCs.

Strengths:

(1) 7T high-resolution MRS is used.

(2) This study combines the behavioral tests, MRS, and fMRI.

Weaknesses:

Major:

In Melnick (2013) IQ scores were measured by the full set of WAIS-III, including all subtests. However, this study only used visual spatial domain of gF. I wonder why only the visuo-spatial subtest was used not the full WAIS-III? I am wondering whether other subtests were conducted and, if so, please include the results as well to have comprehensive comparisons with Melnick (2013).

We thank the reviewer for pointing this out. The decision was informed by Melnick’s findings which indicated high correlations between Surround suppression (SI) and the Verbal Comprehension, Perceptual Reasoning, Working Memory, and Processing Speed Indexes, with correlation coefficients of 0.69, 0.47, 0.49, and 0.50, respectively. It is well-established that the hMT+ region of the brain is a sensory cortex involved in visual perception processing (3D perception). Furthermore, motion surround suppression (SI), a specific function of hMT+, aligns closely with this region's activities. Given this context, the Perception Reasoning sub-ability was deemed to have the clearest mechanism for further exploration. Consequently, we selected the most representative subtest of Perception Reasoning—the Block Design Test—which primarily assesses 3D visual intelligence.” For further clarification, due to these reasons, we conducted only the visuo-spatial subtest.

Minor:

Comments:

In the first revised version, we addressed the following recommendations in the 'Author response' file titled 'Recommendation for the authors.' It seems our response may not have reached you successfully. We would like to share and expand upon our response here:

(1) Table 1 and Table supplementary 1-3 contain many correlation results. But what are the main points of these values? Which values do the authors want to highlight? Why are only p-values shown with significance symbols in Table supplementary 2??

(1.1) What are the main points of these values?

Thank reviewer for pointing this out. These correlations represent the relationship between behavior task (SI/BDT) and resting-state functional connectivity. It indicates that left hMT+ is involved in the efficient information integration network when it comes to BDT task. In addition, left hMT+’s surround suppression is involved in several hMT+ - frontal connectivity. Furthermore, the overlap regions between two task indicates the underlying mechanism.

(1.2) Which values do the authors want to highlight?

Table 1 and Table Supplementary 1-3 present the preliminary analysis results for Table 2 and Table Supplementary 4-6. So, we generally report all value. Conversely, in the Table 2 and Table Supplementary 4-6, we highlight the value which support our main conclusion.

(1.3) Why are only p-values shown with significance symbols in Table Supplementary 2?

Thank you for pointing this out, it is a mistake. We have revised it and delete the significance symbols.

(2) Line 27, it is unclear to me what is "the canonical theory".

We thank reviewer for pointing this out. We have revised “the canonical theory" to “the prevailing opinion” (line 27)

(3) Throughout the paper, the authors use "MT+", I would suggest using "hMT+" to indicate the human MT complex, and to be consistent with the human fMRI literature.

We thank reviewer for pointing this out. We have revised them.

(4) At the beginning of the results section, I suggest including the total number of subjects. It is confusing what "31/36 in MT+, and 28/36 in V1" means.

We thank reviewer for pointing this out. We have included the total number of subjects in the beginning of result section. (line 110, line 128)

(5) Line 138, "This finding supports the hypothesis that motion perception is associated with neural activity in MT+ area". This sentence is strange because it is a well-established finding in numerous human fMRI papers. I think the authors should be more specific about what this finding implies.

We thank reviewer for pointing this out. We have revised it to:” This finding is in line with prior results, which indicates that motion perception is associated with neural activity in hMT+ area, but not in EVC (primarily in V1)” (lines 156-158)

(6) There are no unit labels for all x- and y-axies in Figure 1. I only see the unit for Conc is mmol per kg wet weight.

We thank reviewer for pointing this out. Figure 1 is a schematic and workflow chart, so labels for x- and y-axes are not needed. I believe this confusion might pertain to Figure 3. In Figures 3a and 3b, the MRS spectrum does not have a standard y-axis unit as it varies based on the individual physical conditions of the scanner; it is widely accepted that no y-axis unit is used. While the x-axis unit is ppm, which indicate the chemical shift of different metabolites. In Figure 3c, the BDT represents IQ scores, which do not have a standard unit. Similarly, in Figures 3d and 3e, the Suppression Index does not have a standard unit.

(7) Although the correlations are not significant in Figure Supplement 2&3, please also include the correlation line, 95% confidence interval, and report the r values and p values (i.e., similar format as in Figure 1C).

We thank reviewer for pointing this out. We have revised them and include the correlation line, 95% confidence interval, r values and p values.

(8) There is no need to separate different correlation figures into Figure Supplementary 1-4. They can be combined into the same figure.

We thank reviewer for the suggestion. However, each correlation figure in the supplementary figures has its own specific topic and conclusion. Please notes that in the revised version, we have added a figure showing the EVC (primarily in V1) MRS scanning ROI as Supplementary Figure 1. Therefore, the figures the reviewer is concerned about are Supplementary Figure 2-5. The correlation figures in Supplementary Figure 2 indicate that GABA in EVC (primarily in V1) does not show any correlation with BDT and SI, illustrating that inhibition in EVC (primarily in V1) is unrelated to both 3D visuo-spatial intelligence and motion suppression processing. The correlations in Supplementary Figure 3 indicate that the excitation mechanism, represented by Glutamate concentration, does not contribute to 3D visuo-spatial intelligence in either hMT+ or EVC (primarily in V1). Supplementary Figure 4 validates our MRS measurements. Supplementary Figure 5 addresses potential concerns regarding the impact of outliers on correlation significance. Even after excluding two “outliers” from Figures 3d and 3e, the correlation results remain stable.

(9) Line 213, as far as I know, the study (Melnick et al., 2013) is a psychophysical study and did not provide evidence that the spatial suppression effect is associated with MT+.

We thank reviewer for pointing this out. It was a mistake to use this reference, and we have revised it accordingly. (line 242)

(10) At the beginning of the results, I suggest providing more details about the motion discrimination tasks and the measurement of the BDT.

We thank reviewer for pointing this out. We have included some brief description of task in the beginning of result section. (lines 116-120)

(11) Please include the absolute duration thresholds of the small and large sizes of all subjects in Figure 1.

We thank reviewer for the suggestion. We have included these results in Figure 3.

(12) Figure 5 is too small. The items in plot a and b can be barely visible.

We thank reviewer for pointing this out. We increase the size and resolution of the Figure.

Reviewer #3 (Public Review):

(1) Throughout the manuscript, hMT+ connectivity with the frontal cortex has been treated as an a priori hypothesis/space. However, there is no such motivation or background literature mentioned in the Introduction. Can the authors clarify the necessity of functional connectivity? In other words, can BOLD activity of hMT+ in the localizer task substitute for functional connectivity between hMT+ and the frontal cortex?

(1.1) Throughout the manuscript, hMT+ connectivity with the frontal cortex has been treated as an a priori hypothesis/space. However, there is no such motivation or background literature mentioned in the Introduction. Can the authors clarify the necessity of functional connectivity?

We thank reviewer for pointing this out. We offered additional motivation and background literature in the introduction: “Frontal cortex is usually recognized as the cognitive core region (Duncan et al., 2000; Gray et al., 2003). Strong connectivity between the cognitive regions suggests a mechanism for large-scale information exchange and integration in the brain (Barbey, 2018; Cole et al., 2012).  Therefore, the potential conjunctive coding may overlap with the inhibition and/or excitation mechanism of hMT+. Taken together, we hypothesized that 3D visuo-spatial intelligence (as measured by BDT) might be predicted by the inhibitory and/or excitation mechanisms in hMT+ and the integrative functions connecting hMT+ with frontal cortex (Figure 1a).” (lines 67-74). Additionally, we have included a whole-brain analysis for validation. Functional connectivity reveals the information exchange relationships across regions, enhancing our understanding of how hMT+ and the frontal cortex collaborate when solving visual-spatial intelligence tasks.

(1.2) In other words, can BOLD activity of hMT+ in the localizer task substitute for functional connectivity between hMT+ and the frontal cortex?

We thank the reviewer for this question. The localizer task was used solely for defining the hMT+ MRS scanning area. Functional connectivity was measured using resting-state fMRI. Research has shown that resting-state functional connectivity between the frontal cortex and other ROIs can further reveal the neural mechanisms underlying intelligence tasks (Song et al., 2008).

(2) There is an obvious mismatch between the in-text description and the content of the figure:<br /> "In contrast, there was no correlation between BDT and GABA levels in V1 voxels (figure supplement 1a). Further, we show that SI significantly correlates with GABA levels in hMT+ voxels (r = 0.44, P = 0.01, n = 31, Figure 3d). In contrast, no significant correlation between SI and GABA concentrations in V1 voxels was observed (figure supplement 1b)."

We thank reviewer for pointing this out. We have revised it. The revised version is :” In contrast, there was no correlation between BDT and GABA levels in V1 voxels (figure supplement 2a). Further, we show that SI significantly correlates with GABA levels in hMT+ voxels (r = 0.44, P = 0.01, n = 31, Figure 3d). In contrast, no significant correlation between SI and GABA concentrations in V1 voxels was observed (figure supplement 2b).” (lines 151-156)

(3) The authors' response to my previous round of review indicated that the "V1 ROIs" covered a substantial amount of V3 (32%). Therefore, it would no longer be appropriate to call these "V1 ROIs". I'd suggest renaming them as "Early Visual Cortex (EVC) ROIs" to be more accurate. Can the authors justify why choosing the left hemisphere for visual intelligence task, which is typically believed to be right lateralized?

(3.1) The authors' response to my previous round of review indicated that the "V1 ROIs" covered a substantial amount of V3 (32%). Therefore, it would no longer be appropriate to call these "V1 ROIs". I'd suggest renaming them as "Early Visual Cortex (EVC) ROIs" to be more accurate.

We thank the reviewer for pointing this out. We have revised our description of the MRS scanning ROIs to Early Visual Cortex (EVC). Since the majority of our EVC ROIs are in V1 (around 70%) and almost no V2 was included, we decided to mark the EVC ROIs with the explanation "primarily in V1" for better clarification. This terminology has been widely used to better emphasize the V1-based experimental design.

(3.2) Can the authors justify why choosing the left hemisphere for visual intelligence task, which is typically believed to be right lateralized?

We thank the reviewer for pointing this out. The use of the left MT/V5 as a target was motivated by studies demonstrating that left MT+/V5 TMS is more effective at causing perceptual effects (Tadin et al., 2011). Therefore, we chose to use the left hMT+ as our MRS ROI and maintain consistency across different models' ROIs. Additionally, our results support the notion that the visual intelligence task is right lateralized in the frontal cortex. At the resting-fMRI level, we found that significant ROIs, where functional connectivity is highly correlated with BDT scores, are in the right frontal cortex (Figure 5a, b).

(4) "Small threshold" and "large threshold" are neither standard descriptions, and it is unclear what "small threshold" refers to in the following figure caption. Additionally, the unit (ms) is confusing. Does it refer to timing?<br /> "(f) Peason's correlation showing significant negative correlations between BDT and small threshold."

Thank you for pointing this out; we agree with your suggestion. We have revised the terms “small threshold” and “large threshold” to “duration threshold of small grating” and “duration threshold of large grating”, respectively. The unit (ms) refers to timing. The details are described in the methods section: “The duration was adaptively adjusted in each trial, and duration thresholds were estimated using a staircase procedure. Thresholds for large and small gratings were obtained from a 160-trial block that contained four interleaved 3-down/1-up staircases. For each participant, we computed the correct rate for different stimulus durations separately for each stimulus size. These values were then fitted to a cumulative Gaussian function, and the duration threshold corresponding to the 75% correct point on the psychometric function was estimated for each stimulus size”.

(5) In the response letter, the authors mentioned incorporating the neural efficiency hypothesis in the Introduction, but the revised Introduction does not contain such information.

We thank the reviewer for pointing this out. In our revised version, the second paragraph of the introduction addresses the neural efficiency hypothesis: “The “neuro-efficiency” hypothesis is one explanation for individual differences in gF (Haier et al., 1988). This hypothesis puts forward that the human brain’s ability to suppress irrelevant information leads to more efficient cognitive processing. Correspondingly, using a well-known visual motion paradigm (center-surround antagonism) (Liu et al., 2016; Tadin et al., 2003), Melnick et al found a strong link between suppression index (SI) of motion perception and the scores of the block design test (BDT, a subtest of the Wechsler Adult Intelligence Scale (WAIS), which measures the visuo-spatial component (3D domain) of gF (Melnick et al., 2013). Motion surround suppression (SI), a specific function of human extrastriate cortical region, middle temporal complex (hMT+), aligns closely with this region's activities (Gautama & Van Hulle, 2001). Furthermore, hMT+ is a sensory cortex involved in visual perception processing (3D domain) (Cumming & DeAngelis, 2001). These findings suggest that hMT+ potentially plays a significant role in 3D visuo-spatial intelligence by facilitating the efficient processing of 3D visual information and suppressing irrelevant information. However, more evidence is needed to uncover how the hMT+ functions as a core region for 3D visuo-spatial intelligence.” (lines 51-66)

Recommendations for the authors:

Reviewer #1 (Recommendations for The Authors):

In the Code availability, it states that "this paper does not report original code". It seems weird because at least the code to reproduce the figures from the data should be provided.

Thank you for pointing this out. Almost all figures were created using software such as DPABI, BrainNet, and GraphPad Prism 9.5, which are manually operated and do not require code adjustments. However, for the MRS fitting curve, we can provide our MATLAB code for redrawing the MRS fitting. The code has been uploaded to GitHub.

eLife assessment

This important study combined multiple approaches to gain insight into why rising estradiol levels, by influencing hypothalamic neurons, ultimately lead to ovulation. The experimental data were robust, but evidence for the conclusion that the findings explain how estradiol acts in the intact female was incomplete because of the lack of experimental conditions that better approximate physiological conditions. This work will be of interest to reproductive biologists working on ovarian biology and female fertility.

Reviewer #1 (Public Review):

Summary:

In this work, Qiu and colleagues examined the effects of preovulatory (i.e., proestrous or late follicular phase) levels of circulating estradiol on multiple calcium and potassium channel conductances in arcuate nucleus kisspeptin neurons. Although these cells are strongly linked to a role as the "GnRH pulse generator," the goal here was to examine the physiological properties of these cells in a hormonal milieu mimicking late proestrus, the time of the preovulatory GnRH-LH surge. Computational modeling is used to manipulate multiple conductances simultaneously and support a role for certain calcium channels in facilitating a switch in firing mode from tonic to bursting. CRISPR knockdown of the TRPC5 channel reduced overall excitability, but this was only examined in cells from ovariectomized mice without estradiol treatment. The manuscript has been substantially improved from the initial version by the addition of new experiments and clarification of important figures. Importantly, the overlap of data with previous reports from the same group has been corrected.

Strengths:

(1) Examination of multiple types of calcium and potassium currents, both through electrophysiology and molecular biology.

(2) Focus on arcuate kisspeptin neurons during the surge is relatively conceptually novel as the anteroventral periventricular nucleus (AVPV) kisspeptin neurons have received much more attention as the "surge generator" population.

(3) The modeling studies allow for direct examination of manipulation of single and multiple conductances, whereas the electrophysiology studies necessarily require examination of each current in isolation. Construction of an arcuate kisspeptin neuron model promises to be of value to the reproductive neuroendocrinology field.

Weaknesses:

A remaining weakness in this revised version of the manuscript is that the relevance of the CRISPR experiments is still rather tenuous given that the goal is to understand what happens in the estrogen-treatment condition, and these experiments were performed only in OVX mice. Similar concerns reflect that the computational model examining the effect of E2 infers multiple conductances based on qPCR data and an assumption that the conductances are directionally proportional to the level of gene expression, and then tunes these to the current recordings obtained from OVX mice, without a direct confirmation in OVX+E2 conditions that the model parameters accurately reflect the properties of these currents in the presence of estrogen.

Reviewer #2 (Public Review):

Summary:

Kisspeptin neurons of the arcuate nucleus (ARC) are thought to be responsible for the pulsatile GnRH secretory pattern and to mediate feedback regulation of GnRH secretion by estradiol (E2). Evidence in the literature, including the work of the authors, indicates that ARC kisspeptin coordinate their activity through reciprocal synaptic interactions and the release of glutamate and of neuropeptide neurokinin B (NKB), which they co-express. The authors show here that E2 regulates the expression of genes encoding different voltage-dependent calcium channels, calcium-dependent potassium channels and canonical transient receptor potential (TRPC5) channels and of the corresponding ionic currents in ARC kisspeptin neurons. Using computer simulations of the electrical activity of ARC kisspeptin neurons, the authors also provide evidence of what these changes translate into in terms of these cells' firing patterns. The experiments reveal that E2 upregulates various voltage-gated calcium currents as well as 2 subtypes of calcium-dependent potassium currents while decreasing TRPC5 expression (an ion channel downstream of NKB receptor activation), the slow excitatory synaptic potentials (slow EPSP) elicited in ARC kisspeptin neurons by NKB release and expression of the G protein-associated inward-rectifying potassium channel (GIRK). Based on these results, and on those of computer simulations, the authors propose that E2 promotes a functional transition of ARC kisspeptin neurons from neuropeptide-mediated sustained firing that supports coordinated activity for pulsatile GnRH secretion to a less intense burst-like firing pattern that could favor glutamate release from ARC kisspeptin. The authors suggest that the latter might be important for the generation of the preovulatory surge in females.

Strengths:

The authors combined multiple approaches in vitro and in silico to gain insights into the impact of E2 on the electrical activity of ARC kisspeptin neurons. These include patch-clamp electrophysiology combined with selective optogenetic stimulation of ARC kisspeptin neurons, reverse transcriptase quantitative PCR, pharmacology and CRISPR-Cas9-mediated knockdown of the Trpc5 gene. The addition of computer simulations for understanding the impact of E2 on the electrical activity of ARC kisspeptin cells is also a strength.<br /> The authors add interesting information on the complement of ionic currents in ARC kisspeptin neurons and on their regulation by E2 to what was already known in the literature. Pharmacological and electrophysiological experiments appear of the highest standards and robust statistical analyses are provided throughout. The impact of E2 replacement on calcium and potassium currents is compelling. Likewise, the results of Trpc5 gene knockdown do provide good evidence that the TRPC5 channel plays a key role in mediating the NKB-mediated slow EPSP. Surprisingly, this also revealed an unsuspected role for this channel in regulating the membrane potential and excitability of ARC kisspeptin neurons.

Weaknesses:

The manuscript also has weaknesses that obscure some of the conclusions drawn by the authors.

One is that the authors compare here two conditions, OVX versus OVX replaced with high E2, that may not reflect the physiological conditions under which the proposed transition between neuropeptide-dependent sustained firing and less intense burst firing might take place (i.e. the diestrous [low E2] and proestrous [high E2] stages of the estrous cycle). This is an important caveat to keep in mind when interpreting the authors' findings. Indeed, that E2 alters certain ionic currents when added back to OVX females, does not mean that the magnitude of all of these ionic currents will vary during the estrous cycle.

In addition, although the computational modeling indicates a role of the various E2-modulated conductances in causing a transition in ARC kisspeptin neuron firing pattern, their role is not directly tested in physiological recordings, weakening the link between these changes and the shift in firing patterns.

Overall, the manuscript provides interesting information about the effects of E2 on specific ionic currents in ARC kisspeptin neurons and some insights into the functional impact of these changes. However, some of the conclusions of the work, with regard, in particular, to the role of these changes in ion channels and their implications for the LH surge, are not fully supported by the findings.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this work, Qiu and colleagues examined the effects of preovulatory (i.e., proestrous or late follicular phase) levels of circulating estradiol on multiple calcium and potassium channel conductances in arcuate nucleus kisspeptin neurons. Although these cells are strongly linked to a role as the "GnRH pulse generator," the goal here was to examine the physiological properties of these cells in a hormonal milieu mimicking late proestrus, the time of the preovulatory GnRH-LH surge. Computational modeling is used to manipulate multiple conductances simultaneously and support a role for certain calcium channels in facilitating a switch in firing mode from tonic to bursting. CRISPR knockdown of the TRPC5 channel reduced overall excitability, but this was only examined in cells from ovariectomized mice without estradiol treatment. The patch clamp experiments are comprehensive and overall solid but a direct demonstration of the role of these conductances in being necessary for surge generation (or at least having a direct physiological consequence on surge properties) is lacking, substantially reducing the impact of the findings.

Strengths:

(1) Examination of multiple types of calcium and potassium currents, both through electrophysiology and molecular biology.

(2) Focus on arcuate kisspeptin neurons during the surge is relatively conceptually novel as the anteroventral periventricular nucleus (AVPV) kisspeptin neurons have received much more attention as the "surge generator" population.

(3) The modeling studies allow for direct examination of manipulation of single and multiple conductances, whereas the electrophysiology studies necessarily require examination of each current in isolation. The construction of an arcuate kisspeptin neuron model promises to be of value to the reproductive neuroendocrinology field.

We thank the reviewer for recognizing our comprehensive examination of Kiss-ARH neurons through electrophysiological, molecular and computational modeling of their activity during the preovulatory surge, which as the reviewer pointed out is “conceptually novel.”  We  have bolstered our argument that Kiss1-ARH neurons transition from synchronized firing to burst firing with the E2-mediated regulation of channel expression with the addition of new experiments. We have addressed the recommendations as follows:

Weaknesses:

(1) The novelty of some of the experiments needs to be clarified. This reviewer's understanding is that prior experiments largely used a different OVX+E2 treatment paradigm mimicking periods of low estradiol levels, whereas the present work used a "high E2" treatment model. However, Figures 10C and D are repeated from a previous publication by the same group, according to the figure legend. Findings from "high" vs. "low" E2 treatment regimens should be labeled and clearly separated in the text. It would also help to have direct comparisons between results from low E2 and high E2 treatment conditions.

We have revised Figures 10C and 10D to include new findings (only) on Tac2 and Vglut2 expression in OVX and E2-treated Kiss1ARH.  Most importantly, our E2 treatment regime is clearly stated in the Methods and is exactly the same that was used previously (Qiu, eLife 2016 and Qiu, eLife 2018) for the induction of the LH surge in OVX mice (Bosch, Molecular and Cellular Endocrinology 2013) .

(2) In multiple places, links are made between the changes in conductances and the transition from peptidergic to glutamatergic neurotransmission. However, this relationship is never directly assessed. The data that come closest are the qPCR results showing reduced Tac2 and increased Vglut2 mRNA, but in the figure legend, it appears that these results are from a prior publication using a different E2 treatment regimen.

In the revised Figure 1, we have now included a clear depiction of the transition from synchronized firing driven by NKB signaling in OVX females to burst firing driven by glutamate in E2-treated females. All of the qPCR results in the revised manuscript are new.  We have used the same E2 treatment paradigm as previously published (Qiu, eLife 2018).

(3) Similarly, no recordings of arcuate-AVPV glutamatergic transmission are made so the statements that Kiss1ARH neurons facilitate the GnRH surge via this connection are still only conjecture and not supported by the present experiments.

Using a horizontal hypothalamic slice preparation, we have shown that Kiss1-ARH neurons excite GnRH neurons via Kiss1ARH glutaminergic input to Kiss1AvPV/Pen neurons (summarized in Fig. 12, Qiu, eLife 2016). We did not think that it was necessary to repeat these experiments for the current manuscript.

(4) Figure 1 is not described in the Results section and is only tenuously connected to the statement in the introduction in which it is cited. The relevance of panels C and D is not clear. In this regard, much is made of the burst firing pattern that arises after E2 treatment in the model, but this burst firing pattern is not demonstrated directly in the slice electrophysiology examples.

We have extensively revised Figure 1 to include new whole-cell, current clamp recordings that document burst firing  in  E2-treated, OVX females, which is now cited in the Results.

(5) In Figure 3, it would be preferable to see the raw values for R1 and R2 in each cell, to confirm that all cells were starting from a similar baseline. In addition, it is unclear why the data for TTA-P2 is not shown, or how many cells were recorded to provide this finding.

Before initiating photo-stimulation for each Kiss1-ARH neuron, we adjust the resting membrane potential to -70 mV, as noted  in each panel in Figure 3, through current injections. We have now included new findings on the effects of the T-channel blocker TTA-P2 on slow EPSP in the revised Figure 3. The number of cells tested with each calcium channel blocker is depicted in each of the bar graphs summarizing the effects of the blockers (Figure 3E).

(6) In Figure 5, panel C lists 11 cells in the E2 condition but panel E lists data from 37 cells. The reason for this discrepancy is not clear.

In Figure 5D, we measured the L-, N-, P/Q and R channel currents after pretreatment with TTA-P2 to block the T-type current, whereas in Figure 5C, we measured the total current without TTA-P2.

(7) In all histogram figures, it would be preferable to have the data for individual cells superimposed on the mean and SEM.

In the revised Figures we have included the individual data points for the individual neurons and animals (qPCR). 

(8) The CRISPR experiments were only performed in OVX mice, substantially limiting interpretation with respect to potential roles for TRPC5 in shaping arcuate kisspeptin neuron function during the preovulatory surge.

The TRPC5 channels are most  important for generating slow EPSPs when expression of NKB is high in the OVX state. Conversely, the glutamatergic response becomes more significant when the expression of NKB and TRPC5 channel are muted in the E2-treated state. Therefore, the CRISPR experiments were specifically conducted in OVX mice to maximize the effects.

(9) Furthermore, there are no demonstrations that the CRISPR manipulations impair or alter the LH surge.

In this manuscript, our focus is on the cellular electrophysiological activity of the Kiss1ARH neurons in OVX and E2-treated OVX females. Exploration of CRISPR manipulations related to the LH surge is certainly slated for future  experiments, but these in vivo experiments are  beyond the scope of these comprehensive cellular electrophysiological and molecular studies.

(10) The time of day of slice preparation and recording needs to be specified in the Methods.

We have provided the times of slice preparation and recordings in the revised Methods and Materials.

Reviewer #2 (Public Review):

Summary:

Kisspeptin neurons of the arcuate nucleus (ARC) are thought to be responsible for the pulsatile GnRH secretory pattern and to mediate feedback regulation of GnRH secretion by estradiol (E2). Evidence in the literature, including the work of the authors, indicates that ARC kisspeptin coordinate their activity through reciprocal synaptic interactions and the release of glutamate and of neuropeptide neurokinin B (NKB), which they co-express. The authors show here that E2 regulates the expression of genes encoding different voltage-dependent calcium channels, calcium-dependent potassium channels, and canonical transient receptor potential (TRPC5) channels and of the corresponding ionic currents in ARC kisspeptin neurons. Using computer simulations of the electrical activity of ARC kisspeptin neurons, the authors also provide evidence of what these changes translate into in terms of these cells' firing patterns. The experiments reveal that E2 upregulates various voltage-gated calcium currents as well as 2 subtypes of calcium-dependent potassium currents while decreasing TRPC5 expression (an ion channel downstream of NKB receptor activation), the slow excitatory synaptic potentials (slow EPSP) elicited in ARC kisspeptin neurons by NKB release and expression of the G protein-associated inward-rectifying potassium channel (GIRK). Based on these results, and on those of computer simulations, the authors propose that E2 promotes a functional transition of ARC kisspeptin neurons from neuropeptide-mediated sustained firing that supports coordinated activity for pulsatile GnRH secretion to a less intense firing in glutamatergic burst-like firing pattern that could favor glutamate release from ARC kisspeptin. The authors suggest that the latter might be important for the generation of the preovulatory surge in females.

Strengths:

The authors combined multiple approaches in vitro and in silico to gain insights into the impact of E2 on the electrical activity of ARC kisspeptin neurons. These include patch-clamp electrophysiology combined with selective optogenetic stimulation of ARC kisspeptin neurons, reverse transcriptase quantitative PCR, pharmacology, and CRIPR-Cas9-mediated knockdown of the Trpc5 gene. The addition of computer simulations for understanding the impact of E2 on the electrical activity of ARC kisspeptin cells is also a strength.

The authors add interesting information on the complement of ionic currents in ARC kisspeptin neurons and on their regulation by E2 to what was already known in the literature. Pharmacological and electrophysiological experiments appear of the highest standards. Robust statistical analyses are provided throughout, although some experiments (illustrated in Figures 7 and 8) do have rather low sample numbers.

The impact of E2 on calcium and potassium currents is compelling. Likewise, the results of Trpc5 gene knockdown do provide good evidence that the TRPC5 channel plays a key role in mediating the NKB-mediated slow EPSP. Surprisingly, this also revealed an unsuspected role for this channel in regulating the membrane potential and excitability of ARC kisspeptin neurons.

We thank the reviewer for recognizing that the “pharmacological and electrophysiological experiments appear of the highest standards” and “the addition of the computer modeling for understanding the impact of E2 on the electrical activity of ARC kisspeptin cells is also a strength.  However, we agree with the reviewer that we needed to provide a direct demonstration of “burst-like” firing of Kiss1-ARH neurons, which we have provided in Figure 1. We have addressed the other recommendations as follows:

Weaknesses:

The manuscript also has weaknesses that obscure some of the conclusions drawn by the authors.

One has to do with the fact that "burst-like" firing that the authors postulate ARC kisspeptin neurons transition to after E2 replacement is only seen in computer simulations, and not in slice patch-clamp recordings. A more direct demonstration of the existence of this firing pattern, and of its prominence over neuropeptide-dependent sustained firing under conditions of high E2 would make a more convincing case for the authors' hypothesis.

We have provided  a more direct demonstration of the existence of this firing pattern in the whole-cell current clamp experiments in the revised Figure 1.

In addition, and quite importantly, the authors compare here two conditions, OVX versus OVX replaced with high E2, that may not reflect the physiological conditions (the diestrous [low E2] and proestrous [high E2] stages of the estrous cycle) under which the proposed transition between neuropeptide-dependent sustained firing and less intense burst firing might take place. This is an important caveat to keep in mind when interpreting the authors' findings. Indeed, that E2 alters certain ionic currents when added back to OVX females, does not mean that the magnitude of these ionic currents will vary during the estrous cycle.

We have published that the magnitude of the slow EPSP, which is TRPC5 channel mediated, varies throughout the estrous cycle with the slow EPSP reaching a maximal amplitude during diestrus, which was significantly reduced during proestrus,  similar to that found in OVX compared to E2-treated, OVX females (Figure 2, Qiu, eLife 2016).  Moreover, TRPC5 channel mRNA expression,  similar to the peptides, is downregulated by an E2 treatment (Figure 10 this manuscript) that mimics proestrus levels of the steroid (Bosch et al., Mol Cell Endocrinology 2013). Furthermore, the magnitude of ionic currents is directly proportional to the number of ion channels expressed in the plasma membrane, which we have found correlates with mRNA expression. Therefore, it is likely that the magnitude of these ionic currents will vary during the estrous cycle.

Lastly, the results of some of the pharmacological and genetic experiments may be difficult to interpret as presented. For example, in Figure 3, although it is possible that blockade of individual calcium channel subtypes suppresses the slow EPSP through decreased calcium entry at the somato-dendritic compartment to sustain TRPC5 activation and the slow depolarization (as the authors imply), a reasonable alternative interpretation would be that at least some of the effects on the amplitude of the slow EPSP result from suppression of presynaptic calcium influx and, thus, decreased neurotransmitter and neuropeptide secretion. Along the same lines, in Figure 12, one possible interpretation of the observed smaller slow EPSPs seen in mice with mutant TRPC5 could be that at least some of the effect is due to decreased neurotransmitter and neuropeptide release due to the decreased excitability associated with TRPC5 knockdown.

The reviewer raises a good point, but our previous findings clearly demonstrated that chelating intracellular calcium with BAPTA in whole-cell current clamp recordings abolishes the slow EPSP and persistent firing (Qiu et al., J. Neurosci 2021), which we have noted is the  rationale for dissecting out the contribution of T, R, N, L and P/Q calcium channels to the slow EPSP in our current studies.  The revised Figure 3 also includes the effects of T-channel blocker.

However, to further bolster the argument for the post-synaptic contribution of the calcium channels to the slow EPSP  and eliminate the potential presynaptic effects of the calcium channel blockers on the postsynaptic slow EPSP amplitude, which may result from reduced presynaptic calcium influx and subsequently decreased neurotransmitter release, we have utilized an additional strategy. Specifically, we have measured the response to the externally administered TACR3 agonist senktide under conditions in which the extracellular calcium influx, as well as neurotransmitter and neuropeptide release, are blocked (revised Figure 3).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The use of optogenetics in Figure 3 to trigger the slow EPSP could be better clarified in the text.

We have clarified in the Methods the optogenetic protocol for generating the slow EPSP, which we have published previously (Qiu et al., eLife 2016; eLife 2018, J. Neurosci 2021).

(2) The citation for Figure 4C in the text does not match what is shown in the figure.

Figure 4C has been removed in the revised manuscript.

(3) Figure 5 - it would be clearer to have panel D labeled as "model results" or similar to distinguish it from the slice recording data.

Panel D has been labeled as "Model results”.

(4) The text in lines 191-197 in the Results may be better suited to the Discussion.

We have modified the text in order to present the new findings without the discussion points.

(5) It is somewhat confusing to have figure panels cited out of order in the main text (e.g., 7H before 7G and 8H before 8G).

We have edited the text to report the findings in the proper order of the panels in Figures 7 and 8.

Reviewer #2 (Recommendations For The Authors):

- The observations that E2 treatment of OVX mice has an effect on the magnitude of a number of ionic currents does not necessarily mean that these changes will be seen during the estrous cycle, in response to fluctuations in circulating E2 concentrations. Experiments comparing either different estrous cycle stages or OVX mice treated with low or high E2 would be required to gain insight into this question. As such, the relevance of the authors' findings (however interesting these are as they stand) to any potential physiological endocrine/reproductive state transition is questionable, in the reviewer's opinion. The authors should acknowledge this important caveat and moderate the interpretations of their findings and the conclusions of their manuscript accordingly.

We have published that the magnitude of the slow EPSP, which is TRPC5 channel mediated, varies throughout the estrous cycle with the slow EPSP being large during diestrus and significantly reduced during proestrus,  similar to that found in OVX compared to E2-treated, OVX females (Figure 2, Qiu, eLife 2016).  Moreover, TRPC5 channel mRNA expression,  similar to the peptides, is downregulated by an E2 treatment (Figure 10 this manuscript) that mimics proestrus levels of the steroid (Bosch et al., Mol Cell Endocrinology 2013). Furthermore, the magnitude of ionic currents is directly proportional to the number of ion channels expressed in the plasma membrane, which we have found correlates with mRNA expression. Therefore, it is likely that the magnitude of these ionic currents will vary during the estrous cycle.

- The bursting firing pattern that the authors refer to and postulate will favor glutamate release under high E2 conditions is only seen in the computer simulations, not in patch-clamp recordings in brain slices (see also comment below). This substantially weakens some of the conclusions of the manuscript. Unless the authors can convincingly demonstrate a change in ARC kisspeptin firing pattern in response to increasing E2 using electrophysiology, these conclusions should be moderated.

We now include examples of burst firing activity under E2-treatment conditions in Figure 1 and have included summary figure (pie chart) documenting that a significant percentage of cells exhibit this activity with E2 treatment.  

Other comments:

- Title: "E2 elicits distinct firing patterns" is not shown in this work. As such, the title needs to be revised.

We now show these distinct firing patterns in Figure 1, so we think the wording in the title is an accurate reflection of our findings. 

- Abstract: some of the interpretations are overstated, in the reviewer's opinion.

Line 23, "... elevating the whole-cell calcium current and contributing to high-frequency firing" should be moderated, as what is shown by the authors is that blockade of calcium channel subtypes suppresses the slow EPSP and associated firing, the frequency of which is not reported (see also a later comment).

We now include examples of burst firing activity under E2-treatment conditions in Figure 1 and have modified the abstract to state “high frequency burst firing.”

Lines 26-28, that "mathematical modeling confirmed the importance of TRPC5 channels for initiating and sustaining synchronous firing, while GIRK channels, activated by Dyn binding to kappa opioid receptors, were responsible for repolarization" is simply not what the simulations show, in the reviewer's opinion. Indeed, there is no consideration of synchronous activity in the model, which simulates the firing of a single ARC kisspeptin neuron. Further, the model shows that TRPC5 can contribute to overall excitability (firing in response to current injection, Figure 12G) and that increasing TRPC5 conductance increases firing in response to NKB while this is decreased by adding GIRK conductance to the model (Figure 13A). Therefore, considerations of the importance of TRPC5 channels in initiating synchronous firing and the role of Dyn A-induced GIRK activity should not be included in the interpretations of the mathematical simulations.

The significance of synchronization lies in the fact that when neuronal networks synchronize, the behavior of each neuron within the network becomes identical. In such scenarios, the firing of a single neuron mirrors the activity of the entire neuronal network. Consequently, our model simulations, based on a single-cell neuronal model, can be utilized to make reliable inferences about synchronized neuronal activity.

Lines 31-33 (also lines 92-95), that "the transition to burst firing with high, preovulatory levels of E2 facilitates the GnRH surge through its glutamatergic synaptic connection to preoptic Kiss1 neurons" is not supported by the experiments (physiologic or computational) described in the manuscript, and is, therefore, only speculative. These statements should be removed throughout the manuscript.

Previously, we (Qiu et al., (eLife 2016) documented a direct glutamatergic projection from Kiss1-ARH neurons to Kiss1-AVPV/PeN neurons.  Moreover, Lin et al. (Frontiers Endocrinology 2021) demonstrated that low frequency stimulation of Kiss1-ARH:ChR2 neurons, that is known to only release glutamate, boosts the LH surge, and in a follow-up paper the O’Byrne lab blocked this stimulation with ionotropic glutamate antagonists (Shen et al., Frontiers in Endocrinology 2022).  We have included these references in the Introduction and Discussion, but we did not think that it was necessary to cite these papers in the Abstract.  However, we have re-worded this final statement in the Abstract to: “the transition to burst firing with high, preovulatory levels of E2 would facilitate the GnRH surge….” 

- Introduction: the usefulness of Figure 1 is questionable. From reading the figure legend, it is the reviewer's understanding that panels A and B are published elsewhere (there is no description of methods or results in the manuscript). Further, panels C and D are meant to illustrate that ARC kisspeptin neurons display different types of firing in OVX vs E2-treated OVX mice. The legend to C indicates that the trace illustrates "synchronous firing" but shows one cell (how can this be claimed as synchronous?) - the legend to D indicates that the trace "demonstrates" burst firing in ARC kisspeptin neurons. This part of the figure is, in the reviewer's opinion, misleading because these are only two examples (no quantifications or replicates are provided) obtained by stimulating firing in two different endocrine conditions by two different agonists. The "demonstration" of differential firing patterns would require a thorough examination of firing patterns in response to current injections (as in Figure 12 E-F) or in response to the two agonists, under the different hormonal conditions.

Figure 1 has now been completely revised to include new data documenting the different firing patterns.  The methods detailing these experiments can be found in the Material and Methods section.

The introduction presents a rather incomplete picture of what is known regarding how ARC kisspeptin neurons might coordinate their activity to drive episodic GnRH secretion, and it omits published work showing that blockade of glutamate receptors (in particular AMPA receptors) decreases ARC kisspeptin neuron coordinated activity in the brain slices and in vivo and suppresses pulsatile GnRH/LH secretion in mice.

If we are not mistaken, the reviewer is referring to fiber photometry recordings of GCaMP activity, which we cite in the Discussion.  However, for the Introduction we tried to “set the stage” for our studies on measuring the individual channels underlying the different firing patterns and how they are regulated by E2.

The introduction is also quite long with extensive descriptions of previous work by the authors and in other brain areas that would be better suited for the discussion.

Again, we are trying to rationalize why we focused on particular ion channels based on the literature.

- Results: lines 129-132 should be moderated, as whether calcium channels increase excitability or facilitate TRPC5 channel opening has not been directly assessed here.

High frequency optogenetic stimulation of Kiss1-ARH neurons and NKB through its cognate receptor (TACR3) activates TRPC 5 channels (Qiu et al., eLife 2016; J. Neurosci 2021). BAPTA prevents the opening of TRPC5 channels and abrogates the slow EPSP following high frequency stimulation.  Figure 3 documents that inhibition of voltage-activated calcium channels attenuates the slow EPSP, which results in a decrease in excitability.

Lines 145-146, one limitation of this experiment is that blockade of calcium channel subtypes will not only affect calcium entry and subsequent actions of calcium on TRPC5 channels but also impair the release of neurotransmitters and neuropeptides from kisspeptin neurons. The interpretation that "calcium channels contribute to maintaining the sustained depolarization underlying the slow EPSP" needs, therefore, to be moderated as it is not possible to extract the direct contribution of calcium channels to the activation of TRPC5 channels from these experiments.

We cited our previous findings documenting that chelating intracellular calcium with BAPTA abolishes the slow EPSP and persistent firing (Qiu et al., J Neurosci 2021).  However, to eliminate the potential effects of calcium channel blockers on the slow EPSP amplitude, which may result from reduced presynaptic calcium influx and subsequently decreased neurotransmitter and neuropeptide secretion, we adopted a different strategy by comparing responses between Senktide and Cd2+ plus Senktide. Our findings revealed that the non-selective Ca2+ channel blocker Cd2+ significantly inhibited Senk-induced inward current (Figures 3F-H).

Panel C should be removed from Figure 4, as it is published elsewhere.

Figure 4C has been removed.

Lines 168-169, "...E2 treatment led to a significant increase in the peak calcium current density in Kiss1ARH neurons, which was recapitulated as predicted by our computational modeling..." How did the model "predict" this increase in calcium current density? As no information is provided in the methods or supplementary information as to how the effect of E2 was integrated into the model, the authors will need to provide additional narration in the text to explain this statement. The "T-channel inflection" referred to in the figure legend will also need to be explained. Lastly, in Figure 5C, the current density unit should be pA/pF. 

We have added text in the supplementary information to explain how we used the qPCR and electrophysiological data to inform the model regarding the effect that E2 has on the various ionic currents and noted in the Figure 13 legend that the increase/decrease in the conductances is physiologically mediated by E2. We have eliminated the T-channel inflection point (Figure 5D) and corrected the current density label (Figure 5C).

Lines 198-199, please clarify "E2 does not modulate calcium channel kinetics directly but rather alters the mRNA expression to increase the conductance".

We have clarified that “that long-term E2 treatment does not modulate calcium channel kinetics but rather alters the mRNA expression to increase the calcium channel conductance” by referring to the specific figures (i.e., Figures 4, 6) in a previous sentence.

Figures 7 and 8 titles do not accurately reflect the contents: there is nothing about repolarization in the experiments illustrated in Figure 7 or Figure 8. The sample sizes (3 to 4 cells) are also quite small for these experiments.

We have modified the Figure titles per the reviewer’s comments and increased the cell numbers.

The title of Figure 9 also does not fully reflect the figure's contents. Although panel G does suggest that the M current contributes to regulating the membrane potential, the reviewer's reading of this figure panel is that the fractional contribution of the M current does not vary during a short burst of action potentials. The suggestion that "KCNQ channels play a key role in repolarizing Kiss1ARH neurons following burst firing" (line 272) and the statement that "our modeling predicted that M-current contributed to the repolarization following burst firing" (line 273) should be revised accordingly.

The point is that the M-current contributes, albeit a small fraction, to the repolarization during burst firing.

Line 288, please indicate what figure informs this statement.

We have revised the statement since the modeling (Figure 13) comes later in the Results.

Line 311-313, this sentence only superficially describes the simulation, in the reviewer's opinion. Does the model inform on how TRPC5 channels/currents do that? The supplementary information indicates that there is a tone of extracellular neurokinin B embedded in the model. This is important information that should be clearly stated in the manuscript. The authors should also consider discussing the influence of this neurokinin B tone on the contribution of TRPC5 to cell excitability. As a neurokinin B tone in the extracellular space will likely alter the firing of kisspeptin neurons in the model, readers will likely need more information about all this.

In our current ramp simulations of the model (Fig 12 G&H) there is no involvement of neurokinin B (i.e., the NKB parameter  is set to zero), and the effect on the rheobase is solely due to the decrease of the TRPC5 conductance.  In the model, TRPC5 channels are activated by intracellular calcium levels and are therefore contributing to cell excitability even in the absence of extracellular NKB. The NKB tone is used for the simulations presented in Figure 13 where we vary the TRPC5 conductance under saturating levels of extracellular NKB.

Lines 316-318 also read as quite superficial. More explanations of what is illustrated in Figure 13 are needed. In particular, it is unclear from the methods and supplementary information what the different ratios of conductances in OVX+E2 vs in OVX are and how they were varied in the model. Furthermore, it is unclear to the reviewer how the outcome of these simulations matches the authors' postulate that E2 enables a transition to a burst firing pattern that favors glutamate release. Looking at simulated firing in Figure 13B, E2 (by increasing calcium conductances) would tend to enable high-frequency firing within bursts (nearing 50 Hz by eye) and high burst rates (approximately 4 bursts per second), which the reviewer would argue might be expected to cause significant neuropeptide release in addition to that of glutamate.

We have added to the text: “Furthermore, the burst firing of the OVX+E2 parameterized model was supported by elevated h- and Ca 2+-currents (Figure 13B) as well as by the high conductance of Ca2+ channels relative to the conductance of TRPC5 channels (Figure 13C).” We have also provided in the Supplemental Information (Table of Model Parameters) the specific conductances in the OVX and OVX+E2 state and how they are varied to produce the model simulations.

Granted the high frequency firing during a burst could release peptide, but in the E2-treated, OVX females the expression of the peptides are at “rock bottom.”  Therefore, the sustained high frequency firing during the slow EPSP in the OVX state would generate maximum peptide release.

In Figure 13C, the reviewer is unclear on the ranges of TRPC5 conductances shown. The in vitro experiments suggest that E2 suppresses Trpc5 gene expression and might suppress TRPC5 currents. The ratio of gTRPC5(OVX+E2)/gTRPC5(OVX) should, thus, be <1.0. This is not represented in the parameter space provided, making the interpretation of this simulation difficult. Please clarify what the effect of decreasing gTRPC5 will be on firing patterns in the model.

Thank you for pointing this typographical error.  The ratio should be gTRPC5 (OVX)/TRPC5(OVX + E2) for the X-axis.

- Discussion: many statements and conclusions are overreaching and need to be revised; for example lines 320-322, 329-330, 335-338, 369, 371-373, 391-394, 463-464, and 489-494;

We have tempered these statements, so they are not “overreaching.”

Lines 489-494: the authors should integrate published observations that i) ablation of ARC kisspeptin neurons results in increased LH surges in mice and rats and that ii) optogenetic stimulation of ARC kisspeptin fibers in the POA is only effective at increasing LH secretion in a surge-like manner when done at high frequencies (20 Hz), in their discussion of the role of ARC kisspeptin neurons and their firing patterns in the preovulatory surge.

We have included the paper from the O’Byrne lab (Shen et al. Frontiers in Endocrinology 2022) in the Discussion. However, the Mittleman-Smith paper (Endocrinology, 2016) ablating KNDy neurons using NK3-saporin not only targeted KNDy neurons but other arcuate neurons that express NK3 receptors.  Therefore, we have not cited it in the Discussion.

eLife assessment

This important study introduces the MRAD database, an advancement in Alzheimer's disease research that provides a powerful tool for evaluating risk and protective factors through Mendelian randomization analysis. The evidence supporting the database's utility is solid, with findings backed by robust data, though addressing methodological concerns and ensuring more rigorous validation of associations would further strengthen its impact. This resource represents a significant leap forward in the field, offering unprecedented opportunities for researchers and clinicians to uncover key insights into Alzheimer's etiology, potentially revolutionizing how Alzheimer's research is approached and accelerating the discovery of new prevention strategies and treatments.

Reviewer #1 (Public Review):

Summary:

An online database called MRAD has been developed to identify the risk or protective factors for AD.

Strengths:

This study is a very intriguing study of great clinical and scientific significance that provided a thorough and comprehensive evaluation with regard to risk or protective factors for AD. It also provided physicians and scientists with a very convenient, free as well as user-friendly tool for further scientific investigation.

Comments on revised version:

The authors have resolved all of my previous comments. It's a decent paper worth to be published in this field.

Reviewer #2 (Public Review):

Summary:

This MR study by Zhao et al. provides a comprehensive hypothesis-free approach to identifying risk and protective factors causal to Alzheimer's Disease (AD).

Strengths:

The study employs a comprehensive, hypothesis-free approach, which is novel over traditional hypothesis-driven studies. Also, causal associations between risk/protective factors and AD were addressed using genetic instruments and analysis.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

An online database called MRAD has been developed to identify the risk or protective factors for AD.

Strengths:

This study is a very intriguing study of great clinical and scientific significance that provided a thorough and comprehensive evaluation with regard to risk or protective factors for AD. It also provided physicians and scientists with a very convenient, free as well as user-friendly tool for further scientific investigation.

We thank the reviewer for the conclusion and positive comments.

Weaknesses:

(1) Comment: The paper mentions that the MRAD database currently contains data only from European populations, with no mention of data from other populations or ethnicities. Given potential differences in Alzheimer's Disease (AD) across different populations, the limitations of the data should be emphasized in the discussion, along with plans to expand the database to include data from more racial and geographic regions.

Thank you for your valuable comment. Further information regarding the limitations of populations is provided in the Conclusions section (page 19).

The newly added text describing the limitations of populations is as follows:

“However, in this study, since the GWAS datasets for both the exposure and the outcome traits (AD) selected were obtained from the public database (MRC IEU OpenGWAS), where the GWAS datasets for AD are only of European population, and since we use the TwoSampleMR, which requires that the populations for the exposure trait and the outcome trait be the same to satisfy the requirement for a control variable, this study currently has certain limitations in terms of population. We initiated a Mendelian randomization study on AD at clinical hospitals in China and are currently in the sample collection stage to address the limitations. In the future, we will integrate data from more populations and keep updating new progresses in AD research to explore its potential differences in different populations.”

(2) Comment: Sufficient information should be provided to clarify the data sources, sample selection, and quality control methods used in the MRAD database. Readers may expect more detailed information about the data to ensure data reliability, representativeness, and research applicability.

Thank you for your helpful suggestion. We appreciate you taking time and making effort in reviewing our manuscript and thank you for your insightful comments. We agree that adding more details is essential to make the manuscript more reliability, representativeness, and research applicability.

The newly added text describing more detailed information about the data is as follows:

(1) Sufficient information about data sources and sample selection (in the Data sources section of Methods section, page 8):

“Exposure traits

Inclusion criteria: datasets of the European population.

Exclusion criteria: (i) eQTL-related datasets; (ii) AD-related datasets.

“In this study, the GWAS datasets selected were derived from 42,335 GWAS datasets in the public database (MRC IEU OpenGWAS, https://gwas.mrcieu.ac.uk/). Based on the above inclusion and exclusion criteria, 19,942 eQTL-related datasets were excluded first, leaving 22,393 GWAS datasets. Next, the datasets with the European population were selected, and 18,117 GWAS datasets were obtained. Finally, 20 AD-related datasets were excluded; 18,097 GWAS datasets were obtained at the end as the exposure traits of this study (See Table S1 for basic information).

Outcome traits

Inclusion criteria: (i) datasets of patients with AD with complete information and clear data sources; (ii) datasets of the European population.

Exclusion criteria: (i) Number of SNPs <1 million; (ii) datasets with unspecified sex; (iii) datasets with a family history of AD; (iv) datasets with dementia.

Based on the above criteria, 16 GWAS datasets of outcome traits were selected from the MRC IEU OpenGWAS database, comprising datasets of AD from Alzheimer Disease Genetics Consortium (ADGC), Cohorts for Heart and Aging Research in Genomic Epidemiology Consortium (CHARGE), The European Alzheimer’s Disease Initiative (EADI), and Genetic and Environmental Risk in AD/Defining Genetic, Polygenic and Environmental Risk for Alzheimer’s Disease Consortium (GERAD/PERADES) 2019 (ieu-b-2); AD from Benjamin Woolf 2022 (ieu-b-5067); AD from International Genomics of Alzheimer's Project (IGAP) 2013 (ieu-a-297) as the datasets of main outcome traits for AD, as well as 13 datasets from FinnGen biobank 2021 corresponding to various AD subtypes, referred to as AD-finn subtypes. (as shown in Figure 2).”

(2) Sufficient information about quality control methods (in the Statistical models for causal effect inference section of Methods section, page 9-10:

“A random-effects IVW model was used in this study as the major analysis method to uncover potential risk or protective factors for AD. The random-effects IVW model as the gold standard for MR studies, its principle is to calculate the inverse of the variance of each IV as its weight, assuming all IVs are valid. The regression does not include an intercept term, and the final result is the weighted average of the effect estimates from all IVs [34]. This model indicates that the true effect values may vary across different studies due to both sampling error and the heterogeneity of the true effect. The weight of each study is jointly determined by its inverse variance and the estimated heterogeneity variance. Thus, as long as there is no pleiotropy, even when there is significant heterogeneity (p < 0.05), this method remains the best MR model.

To assess the robustness of the IVW results, sensitivity analysis was performed using six additional models: (i) MR-Egger: MR-Egger’s biggest difference from IVW is that it considers the intercept term during regression to evaluate bias caused by horizontal pleiotropy. The intercept represents the magnitude of horizontal pleiotropy, with a value close to 0 indicating minimal pleiotropy. The primary purpose is to detect and correct for horizontal pleiotropy. Thus, when significant horizontal pleiotropy is observed (p < 0.05), this method is preferred [35,36]. (ii) Weighted median: The weighted median method is a technique for evaluating causal relationships using a majority of genetic variants (SNPs). If at least 50% of the SNPs are valid IVs, the median of the causal estimates will tend toward the true causal effect. This method provides an unbiased estimate (i.e., the “majority validity” assumption) [37]. (iii) Simple mode: Involves comparing the frequencies or proportions of genotypes or phenotypes between control and experimental groups. Moreover, it can illustrate whether the observed differences in genotypes or phenotypes between the two groups are statistically significant. (iv) Weighted mode: The weighted mode method is a technique for combining multiple Mendelian randomization estimates. This method assigns weights to the causal effect estimates of different genetic variants on the trait and then takes the weighted mode as the final estimate of the causal effect. In genetic variant estimates, the method can decrease bias caused by outliers. (v) Maximum likelihood: This method is used when it is known that a random sample follows a particular probability distribution; however, the specific parameters of that distribution remain unknown, and it involves conducting multiple experiments, observing the results, and using those results to infer the approximate values of the parameters [38]. (vi) Penalized weighted median: An enhanced version of the weighted median estimate that provides a consistent estimate of the causal effect. (vii) Heterogeneity and horizontal pleiotropy assessment use the heterogeneity tests [39] and Egger intercept tests [40], respectively.”

(3) Comment: While the authors mention that the MRAD database offers interactive visualization interfaces, the paper lacks detailed information on how to interpret and understand these visual results. Guidelines on effectively using these visualization tools to help researchers better comprehend the data are essential.

Thank you very much for your feedback, as we believe that our manuscript has been improved substantially as a result of your input.  Owing to space constraints, the MRAD database user guide is included in the Supplementary Material. Meanwhile, for better understanding, the subheading of the relevant content in the Supplementary Material has been revised to “MRAD User Guide” (see Supplementary Material for details, page 11). Furthermore, considering user-friendliness, the user guide has been integrated into the database and can be accessed directly from the homepage by clicking on the “User Guide” module.

(4) Comment: In the conclusion section of the paper, it is advisable to explicitly emphasize the practical applications and potential clinical significance of the MRAD database. The paper should articulate how MRAD can contribute to the early identification, diagnosis, prevention, and treatment of AD and its potential societal and clinical value more clearly.

Thank you for pointing this out. In the Discussion section of the revised manuscript, we have now added how MRAD can contribute to the early identification, diagnosis, prevention, and treatment of AD and its potential societal as well as clinical value. And we reorganized the structure of Discussion section to make the text easier to understand, which could be helpful to further clarify the significance of MRAD. (page 15)

The newly added text describing the practical applications and potential clinical significance of the MRAD database is as follows:

“(i) The current methods for identifying AD mainly rely on assessment scales, cerebrospinal fluid (CSF) examinations, and brain PET/MRI. However, assessment scales can be biased by factors such as the anxiety and nervousness of the subjects. CSF examinations require an invasive lumbar puncture, leading to low patient acceptance. PET/MRI scans are expensive and have limited equipment accessibility. These limitations restrict early AD identification. Thus, there is a pressing clinical need for readily available, time- and cost-effective, and accurate detection methods. In this study, the Medical laboratory science and Molecular trait used could be less expensive, faster to detect, easier to operate, and more accessible for widespread adoption. They hold great value for early AD identification and have the potential to become crucial tools for identifying AD in the future. (ii) Imaging acts as a powerful assistive tool for diagnosing Alzheimer’s disease. Traditional imaging examinations mainly depict changes in the brain’s macroscopic structure, while research on microstructural changes in disease-related areas is relatively limited. Studies have demonstrated that microstructural neurodegenerative processes are extensive and pronounced during AD progression. Our study results cover traditional macroscopic neuroimaging results and reveal numerous potential causal relationships between brain microstructure and AD. The combination of macroscopic and microstructural insights will provide more valuable information for clinical diagnosis. (iii) Clarifying patient’s disease, past history, and family history can aid in preventing AD at an early stage, and prevention of AD could be attained through monitoring anthropometric indicators, improving gut microbiota, and adjusting lifestyle traits. (iv) Currently, the development of new drugs for AD is mainly underscored by Aβ, Tau, and other inhibitors. Since 2000, global pharmaceutical companies have invested hundreds of billions of dollars in the development of new drugs for AD, and these drugs have not yielded successful results. AD drug development has thus been perceived as having the highest failure rate of all drug research, reaching 99.6%. Hence, further research on molecular traits to find new targets and develop new drugs for these targets will provide new pathways for AD treatment.”

(5) Comment: Grammar and Spelling Errors: There are several spelling and grammar errors in the paper. Referring to a scientific editing service is recommended.

We appreciate your comments and suggestions for improving our manuscript. We have now used a professional editing service offered by Taylor and Francis to revise the grammar and language, and we have obtained a certificate of proof, which is attached. Thank you for recognizing our research, we have tried our best to improve the quality of this paper to ensure that it meets the high standards required for publication in of journal elife.

Reviewer #2 (Public Review):

Summary:

This MR study by Zhao et al. provides a comprehensive hypothesis-free approach to identifying risk and protective factors causal to Alzheimer's Disease (AD).

Strengths:

The study employs a comprehensive, hypothesis-free approach, which is novel over traditional hypothesis-driven studies. Also, causal associations between risk/protective factors and AD were addressed using genetic instruments and analysis.

We greatly appreciate the positive feedback regarding the overall quality of our work.

Major comments:

(1) Comment: The authors used the inverse-variance weighted (IVW) model as the primary method and other MR methods (MR-Egger, weighted mean, etc.) for sensitivity analysis. However, each method has its own assumption, and IVW is only robust when pleiotropy and heterogeneity are not severe. Rather than using IVW imprudently across all associations, it would be more appropriate to choose the best MR method for each association based on heterogeneity/Egger intercept tests. This customized approach, based on tests of MR assumption violations, yields more stable and reliable results. For reference, please follow up on work by Milad et al. (EHJ - "Plasma lipids and risk of aortic valve stenosis: a Mendelian randomization study"). This study selected the best MR model for each association based on pleiotropy and heterogeneity tests. Given the large number of tests in this work, I suggest initially screening significant signals using IVW, as done, and then validating the results using multiple MR methods for those signals. It is common for MR estimates from different methods to vary significantly (with some being statistically significant and others not), and in such cases, the MR estimates from the best-fitted model should be trusted and highlighted.

Thank you for your professional comments. We agree that our description of the Statistical models for causal effect inference was not specific enough. Therefore, we have included a new text describing more details about each method’s assumption and supplied a predefined approach to select the best statistical estimation from these methods in the Statistical models for causal effect inference section of Methods section (page 9-10). However, we would like to clarify our analysis method. In this study, the main analysis method used is the IVW random effects model instead of the IVW fixed effects model. The IVW random effects model indicates that the true effect values of different studies may vary, including both sampling error and heterogeneity of the true effect. The weight of each study is jointly determined by its inverse variance and the estimated heterogeneity variance. Thus, as long as there is no pleiotropy, even when there is significant heterogeneity (p < 0.05), this method is still the best MR model. We would like to thank you again for your feedback, as we believe that our manuscript has been improved substantially as a result of your input.

The newly added text describing more details about each method’s assumption and the customized best-fitted model is as follows:

“Statistical models for causal effect inference

A random-effects IVW model was used in this study as the major analysis method to uncover potential risk or protective factors for AD. The random-effects IVW model as the gold standard for MR studies, its principle is to calculate the inverse of the variance of each IV as its weight, assuming all IVs are valid. The regression does not include an intercept term, and the final result is the weighted average of the effect estimates from all IVs [34]. This model indicates that the true effect values may vary across different studies due to both sampling error and the heterogeneity of the true effect. The weight of each study is jointly determined by its inverse variance and the estimated heterogeneity variance. Thus, as long as there is no pleiotropy, even when there is significant heterogeneity (p < 0.05), this method remains the best MR model.

To assess the robustness of the IVW results, sensitivity analysis was performed using six additional models: (i) MR-Egger: MR-Egger’s biggest difference from IVW is that it considers the intercept term during regression to evaluate bias caused by horizontal pleiotropy. The intercept represents the magnitude of horizontal pleiotropy, with a value close to 0 indicating minimal pleiotropy. The primary purpose is to detect and correct for horizontal pleiotropy. Thus, when significant horizontal pleiotropy is observed (p < 0.05), this method is preferred [35,36]. (ii) Weighted median: The weighted median method is a technique for evaluating causal relationships using a majority of genetic variants (SNPs). If at least 50% of the SNPs are valid IVs, the median of the causal estimates will tend toward the true causal effect. This method provides an unbiased estimate (i.e., the “majority validity” assumption) [37]. (iii) Simple mode: Involves comparing the frequencies or proportions of genotypes or phenotypes between control and experimental groups. Moreover, it can illustrate whether the observed differences in genotypes or phenotypes between the two groups are statistically significant. (iv) Weighted mode: The weighted mode method is a technique for combining multiple Mendelian randomization estimates. This method assigns weights to the causal effect estimates of different genetic variants on the trait and then takes the weighted mode as the final estimate of the causal effect. In genetic variant estimates, the method can decrease bias caused by outliers. (v) Maximum likelihood: This method is used when it is known that a random sample follows a particular probability distribution; however, the specific parameters of that distribution remain unknown, and it involves conducting multiple experiments, observing the results, and using those results to infer the approximate values of the parameters [38]. (vi) Penalized weighted median: An enhanced version of the weighted median estimate that provides a consistent estimate of the causal effect. (vii) Heterogeneity and horizontal pleiotropy assessment use the heterogeneity tests [39] and Egger intercept tests [40], respectively.”

(2) Comment: Lines 157-160 mentioned "But to date, AD has been reported as hypothesis-driven MR study based on a single factor, ignoring the potential role of a huge number of other risk factors. Also, due to the high degree of heterogeneity present in AD subtypes, which have different biological and genetic characteristics. Thus, the previous studies cannot offer a systematic and complete viewpoint.". This statement overlooks a similar study published in Molecular Psychiatry ("A Phenome-wide Association and Mendelian Randomization Study for Alzheimer's Disease: A Prospective Cohort Study of 502,493"), which rigorously assessed the effects of 4171 factors spanning 10 different categories on AD using observational analysis and MR. The authors should revise their statement on the novelty of their study type throughout the manuscript and discuss how their work differs from and potentially strengthens previous studies.

Thank you for directing us to this literature. We have read this article carefully. This study shares some similarities with our study but there are significant differences with regards to sample sources and research fields. The study, as mentioned by the reviewer, used the UKB database as its sample source, and analyzed the association between 10 categories (comprising 4,171 factors) and AD, which were sociodemographic, physical measures, lifestyle and environment, health conditions, mental health, medications and operations, cognitive function, sex-specific factors, employment, and early-life factors. However, the study revealed they are restricted by the available variables from the UKB database, which lead to variables such as air pollution, blood glucose measures and so on were not included. Conversely, our study used samples from the MRC IEU OpenGWAS database, the largest open GWAS database globally. Furthermore, our research focus differs, as we primarily investigate the causal relationship between the following 10 categories (comprising 18,097 traits) and AD, which were Disease, Medical laboratory science, Imaging, Anthropometric, Treatment, Molecular trait, Gut microbiota, Past history, Family history, and Lifestyle trait. Most importantly, we have established a database encompassing all MR analysis results, allowing researchers and clinicians worldwide to conveniently and rapidly retrieve AD-associated risk factors via an online open integrated platform (MRAD, https://gwasmrad.com/mrad/).We have now added a new text in the Background section (page 6-7) describing the differences and potential strengthens towards previous studies.

The newly added text describing the differences and novelty towards previous studies is as follows:

“Chen et al. [30] used MR analysis to reveal the causal relationship between AD and factors including sociodemographic and early life status. However, the study revealed they are restricted by the available variables from the UKB database, which lead to variables such as air pollution, blood glucose measures and so on were not included. And also, due to the high degree of heterogeneity present in AD subtypes, which have different biological and genetic characteristics. Thus, the previous studies cannot offer a systematic and complete viewpoint. Our study uses the MRC IEU OpenGWAS database as the sample source for MR analysis to address the aforementioned limitations. The MRC IEU OpenGWAS database, the largest open GWAS database globally, has compiled 42,335 GWAS summary datasets from sources such as the UK Biobank, FinnGen Biobank, and Biobank Japan. Analyzing large-scale datasets will break new ground for MR research on AD.

MR requires a combination of background knowledge in biology, computer science, software studies, and statistics, which often leads to a dilemma where biologists are not well-versed in computer and statistical fields, while computer science experts struggle to adopt a medical biology mindset. Consequently, the vast majority of available GWAS data have not been effectively utilized through MR. Therefore, the construction of a multi-level data platform specifically for AD based on MR analysis of massive GWAS data is of great strategic significance, and it will facilitate researchers and clinicians worldwide to conveniently and rapidly obtain risk factors that are causally associated with AD.”

Reference:

[30] Chen SD, Zhang W, Li YZ, et al. (2023). A Phenome-wide Association and Mendelian Randomization Study for Alzheimer's Disease: A Prospective Cohort Study of 502,493 Participants From the UK Biobank. Biol Psychiatry. 1;93(9):790-801.

(3) Comment: Given the large number of tests, the multiple testing issue is concerning. To mitigate potential false positives, I recommend employing the Bonferroni threshold or FDR. The authors should only interpret exposures that are significant at the Bonferroni threshold.

We sincerely appreciate the reviewer's feedback. Thank you for pointing this out. We have added the results of the Bonferroni correction to the Statistical models for the causal effect inference section of the Methods section (page 10) in response to the reviewer's feedback.

The newly added text describing Bonferroni threshold is as follows:

“The above analyses were performed using the TwoSampleMR[41] package in the R (version 4.1.2) software. Association of exposures with outcomes was assessed using odds ratio (OR) and 95% confidence interval (95% CI), with OR > 1 indicating a positive association (risk factor) and 0 < OR < 1 indicating a negative association (protective factor). Differences with a two-sided p < .05 were considered statistically significant. Furthermore, owing to the relatively large number of exposure and outcome traits included in this study, the multiple testing correction method Bonferroni correction was added to identify significant hits, threshold for Bonferroni-corrected was 0.05 divided by 289,552 tests (p <1.727e-07).”

(4) Comment: In the discussion, the authors should interpret or highlight exposures that remain significant after multiple testing corrections.

Thank you for your valuable comment. In response to reviewer feedback, we have put extra emphasis on the exposures that remained significant after multiple testing corrections in the Discussion section (page 17). We thank you again for your feedback, as we believe that our manuscript has been improved substantially as a result of your input.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Comment: In this study, the authors used the inverse-variance weighted (IVW) model as the major analysis method to perform Mendelian randomization analysis to identify various classes of risk or protective factors for AD, early-onset AD, and late-onset AD. An online database called MRAD has been thereby developed with the assistance of Shiny package. This study is a very intriguing study of great clinical and scientific significance that provided a thorough and comprehensive evaluation with regard to risk or protective factors for AD. It also provided physicians and scientists with a very convenient, free as well as user-friendly tool for further scientific investigation.

I believe this manuscript is great research that is worth publishing with all the comments from the Public Review resolved.

We thank the reviewer for taking the time to read and provide valuable feedback on our manuscript, which allowed us to improve the overall quality of our research. All the comments from the Public Review have been rechecked, and appropriate changes have been made in accordance with the reviewers’ suggestions. Point-by-point responses to all the comments from the Public Review can be found in the above. If there are any further issues, please do not hesitate to let us know, so that we can ensure that our manuscript meets the high standards required for publication.

Reviewer #2 (Recommendations For The Authors):

(1) Comment: In the middle lower left section of the graphical abstract, the overlapping positive (N=63) and overlapping negative (N=16) do not sum to the overlapping number (N=80). Could you clarify if any have both positive and negative effects? Additionally, the font size inside the circular elements is too small to read.

We thank you for raising this issue. We have clarified this in the MRAD utility data mining section of Results section (page 12): A total of 63 exposure traits (risk factors) were positively associated with all the three main outcome traits, while 16 exposure traits (protective factors) were negatively associated with the three main outcome traits, with Ulcerative colitis (ebi-a-GCST000964) being negatively associated with the AD outcome traits of ieu-b-2 and ieu-a-297, and positively associated with the AD outcome traits of ieu-b-5067. Additionally, we apologize for the small, unreadable fonts in the graphical abstract figure. In response to reviewer feedback, we have increased the font size within the figure and enhanced the resolution to improve image readability (page 3).

(2) Comment: The x-axis label ("Alzheimer's disease outcome") should be more descriptive. If published GWAS results are used, indicate this as XXX et al. (2022). Also, specify the AD outcome for each category (e.g., AD, early-onset AD, late-onset AD). The y-axis labels should also be clarified; remove identification codes and retain only the exposure names. Apply the same improvements to Figures 2-8.

We appreciate your comments and suggestions for improving our manuscript.

(i) In response to reviewer feedback, information of published GWAS such as authors and year of publication have now been added to the x-axis labels, as demonstrated in Figure 4 (page 31).

(ii) The outcome IDs are unique. We used these IDs to represent the AD information on the x-axis to maintain a clean and clear figure. The corresponding details for each ID are explained in the Outcome traits section of the Methods section (page 8, as shown in Figure 2). AD_EO refers to early-onset AD, and AD_LO refers to late-onset AD, which are also specified in the Abbreviations (page 4).

(iii) We sincerely appreciate the reviewers’ meticulous feedback. While exposure IDs in this study are unique, exposure names are not. A single exposure name may correspond to multiple IDs, each with a potentially different source of information (e.g., author, year, population sample). We believe obtaining consistent results across multiple IDs further strengthens the reliability of our conclusions. Hence, for better clarity of specific exposure information, the exposure IDs have been retained.

(3) Comment: The results across Figures 1-8 are repetitive and not very informative. Consider other visualizations to condense the information into one or two figures. I would recommend using a Manhattan plot or PheWAS plot concept to effectively display many test results at once. Please display the Bonferroni threshold in the plot as a horizontal line to show which exposures are meaningful after adjusting multiple comparisons.

We appreciate this helpful suggestion. We have now condensed Figures 1–8 into a single figure (as shown in Figure 4). Additionally, we have now displayed the Bonferroni correction results in the sensitivity analysis results figures (as shown in Figure 5, Figure S1-S7).

(4) Comment: Consider placing Figure S1 as Figure 1, condensing Figures 1-8 into Figures 2 and 3, and placing the circular diagrams from Figure S6 as Figure 4.

We appreciate this valuable suggestion. The sequence of the figures has been adjusted.

(5) Comment: Create a main table summarizing robust and consistent exposures for AD that are significant at the Bonferroni threshold for readers. For each exposure, please include estimates from IVW, MR-Egger, weighted median, simple mode, weighted mode, maximum likelihood, and penalized weighted median, along with heterogeneity and horizontal pleiotropy tests. I would also highlight or bold estimates from the best-fit model/MR method to help readers identify the most reliable estimates when estimates from multiple methods are heterogeneous.

We appreciate this helpful suggestion. Owing to the excessive amount of information in the table, we have uploaded the table covering the aforementioned information according to the reviewer’s suggestion as supplementary materials (See Table S2). (i) The corresponding id.exposure that pass the Bonferroni threshold are reflected in red font. (ii) Furthermore, according to the customized best-fitted model (as mentioned in the Statistical models for causal effect inference section of Methods section), when there is no pleiotropy or when pleiotropy is not applicable (less than 3 SNPs), random-effects IVW model is the best model. These corresponding id.exposure are shown in red font with a yellow highlight. (iii) Moreover, according to the customized best-fitted model, when there is pleiotropy, MR-Egger is the best model. These corresponding id.exposure are shown in red font with a green highlight.

(6) Comment: Figures S4-S10: These figures are screenshots of web browsers and may not be worth showing. Consider using tools like Adobe AI or R ggplot to create more refined visualizations that are specific to the research question and improve the message of this work.

Thank you very much for your valuable suggestion in reviewing our manuscript. In this study, Figures S4-S10 are screenshots related to the user guide. We sincerely appreciate the reviewer’s feedback and have revised the subheading of this section to MRAD User Guide to clarify its purpose. Demonstrating both text and figures in this section, we aim to help users understand ways to operate MRAD more intuitively and easily.

(7) Comment: Additionally, please show upfront or highlight results from MR analyses based on R packages, as the author mentioned in the method section. Somehow it's difficult to find results from MR-Egger, weighted median, simple mode, weighted mode, maximum likelihood, and penalized weighted median, along with heterogeneity and horizontal pleiotropy tests in the supplementary materials. Apologies if I missed them. Please ensure these results are clearly presented.

We appreciate your comments and suggestions for improving our manuscript. Thank you for pointing this out. We have added the results of the sensitivity analysis based on R packages (as shown in Figure 5, Figure S1-S7, and Table S2).

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

I am not convinced how this study relates to HIV individual HFpEF, and the study design does not seem to be well thought out. 

This is an important point and we have modified the manuscript as mentioned below in our responses.

The connectivity of the study experiments is loose, and data analysis and conclusions are broadly overstated and misinterpreted.

We have modified the manuscript thoroughly so the data are interpret properly, and the conclusions are stated logically. 

For example the study lacks any measure of diastolic contractile function, and even if performed, the relevance of TNFa treatments to cells in vitro in these immature cell contexts would remain unclear. There is surprisingly no reported molecular analyses of potential mechanisms of the calcium transient changes. The study falls short in molecular detail and instead relies on drug treatments and responses that are hard to interpret with dosages that are not well justified and treatments that are numerous. Unclear what changes in calcium transients mean functionally without a comprehensive assessment of CM biomechanical contraction and relaxation measurements, and this would also require parallel molecular investigations of potential targets of any phenotypes observed.

As mentioned above, we have modified the manuscript so the data are interpret properly, and the conclusions are stated logically. In terms of mechanisms for the observed phenomenon, we agree that this was not the focus of studies, however, we have provided a paragraph in the discussion that covers this topic. Although Decay and downstroke time were utilized as surrogates of cardiomyocyte relaxation, direct biomechanical characterization of contraction was not conducted in this study. While cytosolic calcium concentration is a predominant factor to regulate the cell’s relaxation (Reference 52 in the manuscript), there are several mechanisms to modify the relationship, including the transition of sarcomere protein isoforms to pathogenic ones (Reference 53 in the manuscript) and the stimulation of β-adrenergic receptor on cardiomyocytes (Reference 54 in the manuscript). Since hiPSC-CMs utilized for each study is from iPS cells derived from a single donor, we believe that the patterns of sarcomere protein expression and the regulation of β-adrenergic receptor pathway should be consistent among samples, supporting their effects should be minimum in our system. We also did not elucidate molecular mechanisms underlying prolonged decay time induced by TNF-α and IFN-γ in this study. Lee et al. reported that 25 ng/ml TNFa treatment induced a longer decay portion of the calcium transient and a decreased sarcoplasmic ATPase (SERCA) expression in rabbit cardiomyocytes from pulmonary vein (Reference 55 in the manuscript), suggesting our observation in iPS-CM is also through decreased expression of SERCA though further studies remain conducted.

Calcium transient data need to be better illustrated such as with representative peak tracings. The data overall is with too few samples, particularly given the inherent heterogeneity of iPSCM studies. The iPS-CM system as a model for diastolic dysfunction remains unestablished.

We have now prepared several representative curves of calcium transient and their derivatives in Figure 4 D and E, H and I, and in Figure 1-figure supplement 1B. In terms of the way to collect Ca-transient data, each dot in the bar graphs represents the average of signals obtained from one well of the 96-well plates. About 75K cells were seeded in one well, and we believe that the number of cells integrated in the analyses should be sufficient for the statistical analyses. We modified our manuscript as this system does not quantifying diastolic function directly, but represents Ca measurements that indicate cardiomyocyte relaxation.

There are unclear dose choices for the various ART drugs tested, as well as the other drugs tested such as SGLT2i. Besides the observation that SLC5A2 (SGLT2 target) is not established to be expressed in adult mammalian cardiomyocytes. 

Thank you for the comment. The dose ranges of ART drugs were chosen to extend to 10fold above the IC50 concentrations and reflects the upper range of circulating drug concentration in patients receiving these medications (Reference 36-39 in the manuscript). For SGLT2 inhibitor concentration, we referred to a paper utilizing 1-10 μM dapagliflozin (PMID: 35818731). We conducted a preliminary study to test the effect of 1 and 10 μM of dapagliflozin on the Ca-transient of iPS-CMs, and we found that 1 μM of the drug treatment did not cause changes in Ca-transient. Marfella et al. reported that SLC5A2 (SGLT2) expresses in cardiomyocytes under diabetic condition (PMID 36096423). Since diabetes is associated with low grade systemic inflammation, HIV patients might also express SGLT2 in cardiomyocytes. Taken together, we believe that the dosages of the drugs used in our studies are relevant to the clinical therapeutical usages of the drugs.

HIV plasma samples were not tested for cytokine levels, but this could be done to assess the validity of the final experiments. It is unclear what is being tested with these experiments. 

This is a good point and we agree with the reviewer. However, we had limited amount of the patient serum and could not perform a comprehensive analysis of these samples. Nevertheless, we have added a section in the Discussion section providing some clinical relevance of our findings based on the papers that have assessed cytokine levels in the serum of HIV patients.

The choice of serum controls from a second institution (UCSF) opens up concerns over batch effects unrelated to differences in diastolic dysfunction. However, there were no differences with the Northwestern samples. It is unclear why this data is included as it does not add to the impact of the study. 

In our study, we utilized two sets of HIV patient serum samples from different institutions, supporting that our results can be reproduced. We believe that these results significantly augmented the rigor of our findings.

There are concerns about the quality of the iPS-CMs since there is no cell imaging or molecular analyses. Figure 5 Supplement 1 images are of low quality and low resolution to assess cell quality. Overall the iPS-CM QC data is extremely sparse 

We have now added the representative images of iPS-CMs to Figure 1- figure supplement 1A. Our group has used hiPS-CMs extensively in the past (PMID: 26439715). We also updated Fig 5 Supplement 1 with images with better resolution and added Fig 5 Supplement 2 with magnified images. 

Reviewer2 (Public Review):

However, there are some topics that are not well-connected, and the rationale and hypothesis are not clearly defined beforehand, such as mitochondrial membrane potential, mitochondrial ROS, and angiogenic potential. 

We modified the manuscript so the rationale and hypothesis of the study is clearly stated. 

As the hiPSC cardiomyocytes are treated with various reagents to measure diastolic dysfunction, it is important to confirm whether the treatment time and dose used were sufficient to exert a functional effect. Dose and time-dependent experiments are essential, or at least sufficient citations should be provided for selecting the dose for IFN and TNF. 

We used previous publications for the dosages of the drugs used in our paper (1-4). 

After IFN and TNF treatment, determining the expression levels of molecular markers of DD/HFpEF is crucial. Again, if sufficient evidence is available, it can be cited. 

We have included a section in the discussion to address this issue. Briefly, Lee et al. reported that 25 ng/ml TNFa induces a longer decay of calcium transient and a decrease in sarcoplasmic ATPase (SERCA) expression in rabbit cardiomyocytes from pulmonary vein (PMID 17383682). The prolonged Cadecay time in hiPS-CM with the drug administration may be due to a decrease in SERCA expression and impaired Ca-uptake into sarcoplasmic reticulum.

The Methods section describes TMRE colocalization and immunofluorescence, but no images are provided.

We have performed immunofluorescence of hiPSC-CM with TMRE for the quantification of mitochondrial membrane potential (MMP). 

The concentration of TNF and IFN in patients is critical, which was acknowledged and discussed as a limitation of the study by the authors. Authors should consider this aspect, and if not feasible, clinical reports should be cited to provide a rough estimation of their concentration. 

Thank you for this comment. A new section detailing the points brought up by the Reviewer is now added to discussion.

Recommendation for the authors:

Reviewer #1 (Recommendation for the authors):

I suggest a more comprehensive analysis of diastolic function including biomechanical studies of contraction and diastolic function. I suggest increasing the sample #'s, getting a better characterziation of the cardiomyocytes, their expression profiles, and maturation state. The team should dig more deeply into potential molecular mechanisms of the calcium transient changes. Are there changes in SERCA or other SR factors' phosphorylation state or other molecular explanations for the observed changes? I would remove the serum treatment experiments as they distract since they didn't show differences. These are a few of the suggestions I would have for the team.

Our system for measurement of Ca-transient unfortunately does not allow to obtain data on the cellular biomechanical property. We modified the manuscript so the results are not overstated and that the interpretation is correct. Since each dot in bar-graphs for Ca-transient data represents the average of signals generated from 75 K cells, we believe that the number of cells analyzed was sufficient for the analyses. Although it is not conclusive, previous reports suggested induction of SERCA2A expression by TNF-α treatment in isolated cardiomyocytes, suggesting that the mechanism underlying the prolonged calcium decay time in our model may be due to changes in SERCA levels. We included the data from human serum samples from HIV patients since they provide a platform to assess the effects of HIV patient serum on. We believe that these data convey a significant progress understanding the process of myocardial dysfunction in HIV patients.

References

Amirayan-Chevillard, N., Tissot-Dupont, H., Capo, C., Brunet, C., Dignat-George, F., Obadia, Y., Gallais, H., and Mege, J. L. (2000) Impact of highly active anti-retroviral therapy (HAART) on cytokine production and monocyte subsets in HIV-infected patients. Clinical and experimental immunology 120, 107-112

Fraietta, J. A., Mueller, Y. M., Yang, G., Boesteanu, A. C., Gracias, D. T., Do, D. H., Hope, J. L., Kathuria, N., McGettigan, S. E., Lewis, M. G., Giavedoni, L. D., Jacobson, J. M., and Katsikis, P. D. (2013) Type I interferon upregulates Bak and contributes to T cell loss during human immunodeficiency virus (HIV) infection. PLoS Pathog 9, e1003658

Lau, S. L., Yuen, M. L., Kou, C. Y., Au, K. W., Zhou, J., and Tsui, S. K. (2012) Interferons induce the expression of IFITM1 and IFITM3 and suppress the proliferation of rat neonatal cardiomyocytes. Journal of cellular biochemistry 113, 841-847

Stone, S. F., Price, P., Keane, N. M., Murray, R. J., and French, M. A. (2002) Levels of IL-6 and soluble IL-6 receptor are increased in HIV patients with a history of immune restoration disease after HAART. HIV Med 3, 21-27

eLife assessment

This useful study focuses on heart failure with preserved ejection fraction (HFpFE), common in patients with HIV. Researchers used induced human pluripotent stem cell-derived cardiomyocytes (hiPSC-CMs) to stimulate HEFpEF) and found that inflammatory cytokines alter Ca2+ transients. SGLT2 inhibitors and mitochondrial antioxidants reversed this effect. While the study is incomplete and preliminary, its strength lies in introducing hiPSC-CMs as a tool for investigating HFpEF mechanisms. A major weakness was found to be limited functional assessment relevant to HFpEF.

Reviewer #1 (Public Review):

Summary:

This is a reviewed manuscript submission to better understand mechanisms for why HIV individuals have diastolic dysfunction. Due to a lack of robust animal models, the team developed iPS-CM models to study HFpEF. The revised manuscript has toned down claims regarding diastolic function given the lack of mechanical testing. The team has focused on the altered Ca2+ phenotype, which improves the precision of the claims of the team. There remain questions on the functional relevance of the altered calcium handling given the lack of physiological assays. There also remain some questions about whether SGLT2 protein is expressed in these models without testing it, and whether the effects of SGLT2i could be off-target.

Overall, the revised manuscript is improved. I have no major remaining concerns except that the lack of biomechanical assessments diminishes the significance of the study as altered calcium alone would not be considered sufficient evidence for diastolic dysfunction, which was major task set out to answer by the group.

Reviewer #2 (Public Review):

The authors investigated the role of inflammatory molecules in diastolic dysfunction and screened antiviral and cardioprotective pharmacological agents for their potential to reverse inflammation-mediated diastolic dysfunction. This study focuses on heart failure with preserved ejection fraction (HFpEF) in people living with HIV (PLWH), a condition often challenging to study due to the lack of suitable animal models. Using human induced pluripotent stem cell-derived cardiomyocytes (hiPSC-CMs), researchers simulated HFpEF in vitro. They observed that inflammatory cytokines impaired cardiomyocyte relaxation, mimicking HFpEF, while SGLT2 inhibitors and mitochondrial antioxidants reversed this effect. Exposure to serum from HIV patients did not induce dysfunction in hiPSC-CMs. These findings suggest hiPSC-CMs as a promising model for understanding HFpEF mechanisms and testing potential treatments.

Comments on revised version:

The revised manuscript has been improved satisfactorily. The authors also have addressed all of my concerns.

eLife assessment

This work by Shin et al. demonstrated that a different form of PTH (R25C PTH) generated a comparable anabolic signal to rhPTH 1-34 using a large animal model. This valuable finding may have therapeutic potential in promoting bone formation or the healing process, and the methods seem solid, although there remains a concern regarding the small sample size and surgical procedure.

Reviewer #1 (Public Review):

Summary:

This study, titled "Enhancing Bone Regeneration and Osseointegration using rhPTH(1-34) and Dimeric R25CPTH(1-34) in an Osteoporotic Beagle Model," provides valuable insights into the therapeutic effects of two parathyroid hormone (PTH) analogs on bone regeneration and osseointegration. The research is methodologically sound, employing a robust animal model and a comprehensive array of analytical techniques, including micro-CT, histological/histomorphometric analyses, and serum biochemical analysis.

Strengths:

The use of a large animal model, which closely mimics postmenopausal osteoporosis in humans, enhances the study's relevance to clinical applications. The study is well-structured, with clear objectives, detailed methods, and a logical flow from introduction to conclusion. The findings are significant, demonstrating the potential of rhPTH(1-34) and dimeric R25CPTH(1-34) in enhancing bone regeneration, particularly in the context of osteoporosis.

Weaknesses: There are no major weaknesses.

Reviewer #2 (Public Review):

Summary:

This article explores the regenerative effects of recombinant PTH analogues on osteogenesis.

Strengths:

Although PTH has known to induce the activity of osteoclasts, accelerating bone resorption, paradoxically its intermittent use has become a common treat for osteoporosis. Previous studies successfully demonstrated this phenomenon in vivo, but most of them used rodent animal models, inevitably having a limitation. In this article, the authors tried to address this, using a beagle model, and assessed the osseointegrative effect of recombinant PTH analogues. As a result, the authors clearly observed the regenerative effects of PTH analogues, and compared the efficacy, using histologic, biochemical, and radiologic measurement for surgical-endocrinal combined large animal models. The data seem to be solid, and has potential clinical implications.

Weaknesses:

All the issues that I raised have been resolved in the revision process.

Overall, this paper is well-written and has clarity and consistency for a broader readership.

Reviewer #3 (Public Review):

Summary:

The work submitted by Dr. Jeong-Oh Shin and co-workers aims to investigate the therapeutic efficacy of rhPTH(1-34) and R25CPTH(1-34) on bone regeneration and osseointegration of titanium implants using a postmenopausal osteoporosis animal model.

In my opinion the findings presented are not strongly supported by the provided data since the methods utilized do not allow to significantly support the primary claims.

Strengths:

Strengths include certain good technologies utilized to perform histological sections (i.e. the EXAKT system).

Author response:

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

Reviewer #3:

Comments on current version:

As mentioned in my first review, this work is significantly underpowered for the following reasons: 1) n=4 for each treatment group.; 2) no randomization of the surgical sites receiving treatments; 3) implants surgically inserted without precision/guided surgery. The authors have not addressed these concerns.

On a minor note: not sure why the authors present a methodology to evaluate the dynamic bone formation (line 272) but do not present results (i.e. by means of histomorphometrical analyses) utilizing this methodology.

We sincerely appreciate your thorough review and valuable feedback. We have carefully considered your comments and would like to address them as follows:

As mentioned in my first review, this work is significantly underpowered for the following reasons:

(1) n=4 for each treatment group.;

We acknowledge your concern regarding the limited sample size (n=4 per group). While we understand this may affect statistical power, our choice was influenced by ethical considerations in animal experimentation and resource constraints. Increasing the sample size would undoubtedly strengthen the statistical power of our study. However, the logistical and ethical constraints associated with using a larger number of animals in such invasive procedures were significant limiting factors. Specifically, increasing the number of medium to large experimental animals could raise ethical issues, so we used the minimum number possible. Additionally, our study design was reviewed and approved by the animal IRB, which dictated the minimum number of animals we could use. Nevertheless, we conducted power analysis to ensure that our sample size, although limited, was sufficient to detect significant differences given the high variability typically observed in biological responses. The results obtained from our n=4 samples showed consistent trends and significant differences between groups, indicating the robustness of our findings. I will include this point in the limitations section of the discussion. Thank you.

(2) no randomization of the surgical sites receiving treatments;

Thank you for pointing out this issue. We agree that randomization is essential when considering individual differences and the anatomical variations of the jawbone, such as those found in humans. However, this study is an animal experiment where other conditions were controlled, and the interventions were applied after complete bone healing following tooth extraction. Therefore, the impact of randomization of surgical sites was likely minimal, and it is challenging to determine whether it significantly influenced the experimental results. Of course, twelve female OVX beagles were randomly designated into three groups. (Methods section, line 298) However regarding your concern, we would like to present the robustness of histological results from different surgical sites as shown below. Also we will include this point in the limitations section of the discussion.

Histologic analysis of the different surgical sites showed significant differences in bone formation and osseointegration among the three treatment groups: vehicle control, rhPTH(1-34), and dimeric Cys25PTH(1-34). Goldner trichrome staining (Figure A-C) showed enhanced bone formation in both the rhPTH(1-34) and dimeric Cys25PTH(1-34) groups compared to the vehicle control group. The rhPTH(1-34) group showed the most pronounced bone mass gain around the implant. Both treatment groups showed improved bone-to-implant contact compared to the control group, as indicated by the red arrows.

Masson trichrome staining (Figure D-F) further confirmed these results, showing an increase in bone matrix (blue staining) in the rhPTH(1-34) and dimeric Cys25PTH(1-34) groups, with the dimeric rhPTH(1-34) group showing the most extensive and dense bone formation.

TRAP staining (Figure G-I and G'-I') was used to assess osteoclast activity. Interestingly, both the rhPTH(1-34) and dimeric Cys25PTH(1-34) groups showed an increase in TRAP-positive cells compared to the vehicle control, suggesting enhanced bone remodeling activity. The highest number of TRAP-positive cells was observed in the rhPTH(1-34) group and the highest trabecular number, indicating the most active bone remodeling.

To summarize the results, histological analyses revealed that both rhPTH(1-34) and dimeric Cys25PTH(1-34) treatments significantly enhanced osseointegration and bone formation around titanium implants in a postmenopausal osteoporosis model compared to the control. The rhPTH(1-34) group demonstrated superior outcomes, exhibiting the most substantial increase in bone volume, bone-to-implant contact, and osteoclastic activity, indicating its greater efficacy in promoting bone regeneration and implant integration in this experimental context.

Author response image1.

Histological analysis using Goldner trichrome, Masson trichrome, and TRAP staining

(3) implants surgically inserted without precision/guided surgery. The authors have not addressed these concerns.

The primary purpose of precision guides is to prevent damage to various anatomical structures and to ensure perfect placement at the desired location. Even disregarding the potential inaccuracies of precision guides in actual clinical settings, the primary goal of this animal experiment was not to achieve perfect placement or prevent damage to anatomical structures. Instead, the objective was to histologically measure the integrity of the bone surrounding titanium fixture's platform after pharmacological intervention, ensuring it was fully seated in the alveolar bone. To this end, we secured sufficient visibility through periosteal dissection to confirm the perfect placement of the implant and adhered to the principle of maintaining sufficient mesiodistal distance between each fixture. Using such precision guides in this animal experiment, which is not an evaluation of 'implant precision guides,' could potentially introduce inaccuracies and contradict the experimental objectives. Furthermore, since this experiment was conducted on an edentulous ridge where all teeth had been extracted, achieving the same placement as in the presurgical simulation would be impossible, even with the use of precision guides. Thank you once again for your constructive feedback. We will include this point in the limitations section of the discussion.

On a minor note: not sure why the authors present a methodology to evaluate the dynamic bone formation (line 272) but do not present results (i.e. by means of histomorphometrical analyses) utilizing this methodology.

As the reviewer mentioned, we confirmed that the sentence was included in the Methods section despite the analysis not actually being performed. We sincerely apologize for this oversight and will make the necessary corrections immediately. Thank you very much for your keen observation.

eLife assessment

This is a methodologically state-of-the-art systematic review and meta-analysis of studies that addressed the question of whether the administration of multiple antibiotics simultaneously prevents antibiotic resistance development in individuals. The findings are solid. Rather than providing a precise answer, the synthesis of studies eligible for analysis leads to the conclusion that "our analysis could not identify any benefit or harm of using a higher or a lower number of antibiotics regarding within-patient resistance development." This article is important as it articulates the existing knowledge gap, but also serves as an example for careful future use of the meta-analysis methodology, when existing data just don't allow conclusions.

Reviewer #2 (Public Review):

Summary:

The authors performed a systematic review and meta-analysis to investigate whether the frequency of emergence of resistance is different if combination antibiotic therapy is used compared to fewer antibiotics. The review shows that there is currently insufficient evidence to reach a conclusion due to the limited sample size. High-quality studies evaluating appropriate antimicrobial resistance endpoints are needed.

Strengths:

The strength of the manuscript is that the article addresses a relevant research question which is often debated. The article is well-written and the methodology used is valid. The review shows that there is currently insufficient evidence to reach a conclusion due to the limited sample size. High-quality studies evaluating appropriate antimicrobial resistance endpoints are needed. I have several comments and suggestions for the manuscript.

Weaknesses:

Weaknesses of the manuscript are the large clinical and statistical heterogeneity and the lack of clear definitions of acquisition of resistance. Both these weaknesses complicate the interpretation of the study results.

Comments on latest version:

The authors adressed all the comments that were shared in the previous peer review. I still believe that both clinical and statistical heterogeneity remains a problem with the interpretation of the meta-analysis. However, as the authors state, this is in line with the original research question as formulated on Prospero.

Author response:

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

Reviewer #1 (Public Review):

Major comments: 

My main concern about the manuscript is the extent of both clinical and statistical heterogeneity, which complicates the interpretation of the results. I don't understand some of the antibiotic comparisons that are included in the systematic review. For instance the study by Paul et al (50), where vancomycin (as monotherapy) is compared to co-trimoxazole (as combination therapy). Emergence (or selection) of co-trimoxazole in S. aureus is in itself much more common than vancomycin resistance. It is logical and expected to have more resistance in the co-trimoxazole group compared to the vancomycin group, however, this difference is due to the drug itself and not due to co-trimoxazole being a combination therapy. It is therefore unfair to attribute the difference in resistance to combination therapy. Another example is the study by Walsh (71) where rifampin + novobiocin is compared to rifampin + co-trimoxazole. There is more emergence of resistance in the rifampin + co-trimoxazole group but this could be attributed to novobiocin being a different type of antibiotic than co-trimoxazole instead of the difference being attributed to combination therapy. To improve interpretation and reduce heterogeneity my suggestion would be to limit the primary analyses to regimens where the antibiotics compared are the same but in one group one or more antibiotic(s) are added (i.e. A versus A+B). The other analyses are problematic in their interpretation and should be clearly labeled as secondary and their interpretation discussed. 

Thank you for raising these important points and highlighting the need for clarification. We understand that the reviewer has concerns regarding the following points:

(1) The structure of presenting our analyses, i.e. main analyses and sub-group analyses and their corresponding discussion and interpretation

Our primary interest was whether combining antibiotics has an overarching effect on resistance and to identify factors that explain potential differences of the effect of combining antibiotic across pathogens/drugs. Therefore, pooling all studies, and thereby all combinations of antibiotics, is one of our main analyses. The decision to pool all studies that compare a lower number of antibiotics to a higher number of antibiotics was hence predefined in our previously published study protocol (PROSPERO CRD42020187257).

We indeed, find that heterogeneity is high in our statistical analyses. As planned in our study protocol, we did perform several prespecified sub-group analyses and added additional ones. We now emphasize that several sub-group analyses were performed to investigate heterogeneity (L 119ff): “The overall pooled estimates are based on studies that focus on various clinical conditions/pathogens and compare different antibiotics treatments. To explore the impact of these and other potential sources of heterogeneity on the resistance estimates we performed various sub-group analyses and metaregression.” 

The performed sub-group analyses specifically focused on specific pathogens/clinical conditions (figure 3) or explored heterogeneity due to different antibiotics in comparator arms – as suggested by the reviewer (figure 3B, SI section 6). We find that the heterogeneity remains high even if only resistances to antibiotics common to both arms are considered (SI section 6.1.8). With this analysis we excluded comparisons of different antibiotics (e.g., A vs B+C), such as those between vancomycin and cotrimoxazole named by the reviewer. While we aimed to explore heterogeneity and investigate potential factors affecting the effect of combining antibiotic on resistance, limitations arose due to limited evidence and the nature of data provided by the identified studies. Therefore, interpretability remains also limited for the subgroup analyses, which we highlight in the discussion. (L 186 ff: We accounted for many sources of heterogeneity using stratification and meta-regression, but analyses were limited by missing information and sparse data.) Further, specific subgroup analyses are discussed in more detail in the SI.

(2) Difference in resistance development due to the type of the antibiotics or due to combination therapy?

The reviewer raises an important point, which we also try to make: future studies should be systematically designed to compare antibiotic combination therapy, i.e. identical antibiotics in treatment arms should be used, except for additional antibiotics used in both treatment arms. We already mentioned this point in our discussion but highlight this now by emphasizing how many studies did not have identical antibiotics in their treatment arms. We write in L194ff: “19 (45%) of our included studies compared treatment arms with no antibiotics in common, and 22 studies (52%) had more than one antibiotic not identical in the treatment arms (table 1). To better evaluate the effect of combination therapy, especially more RCTs would be needed where the basic antibiotic treatment is consistent across both treatment arms, i.e. the antibiotics used in both treatment arms should be identical, except for the additional antibiotic added in the comparator arm (table 1).”

Furthermore, we investigated the importance of the type of antibiotics with several subgroup analyses (e.g. SI sections 6.1.8 and 6.1.10). We now further highlight the concern of the type of antibiotics in the result section of the main manuscript, where we discuss the sub-group analysis with no common antibiotics in the treatment arms 131 ff: “Furthermore, a lower number of antibiotics performed better than a higher number if the compared treatment arms had no antibiotics in common (pooled OR 4.73, 95% CI 2.14 – 10.42; I2\=37%, SI table S3), which could be due to different potencies or resistance prevalences of antibiotics as discussed in SI (SI section 6.1.10).” As mentioned above we also perform sub-group analyses, where only resistances of antibiotics common to both arms are considered (SI section 6.1.8). However, as discussed in the corresponding sections, the systematic assessment of antibiotic combination therapy remains challenging as not all resistances against antibiotics used in the arms were systematically measured and reported. Furthermore, the power of these sub-group analyses is naturally a concern, as they include fewer studies. 

Another concern is about the definition of acquisition of resistance, which is unclear to me. If for example meropenem is administered and the follow-up cultures show Enterococcus species (which is intrinsically resistant to meropenem), does this constitute acquisition of resistance? If so, it would be misleading to determine this as an acquisition of resistance, as many people are colonized with Enterococci and selection of Enterococci under therapy is very common. If this is not considered as the acquisition of resistance please include how the acquisition of resistance is defined per included study. Table S1 is not sufficiently clear because it often only contains how susceptibility testing was done but not which antibiotics were tested and how a strain was classified as resistant or susceptible. 

Thank you for pointing out this potential ambiguity. The definition of acquisition of resistance reads now (L 275 ff): “A patient was considered to have acquired resistance if, at the follow-up culture, a resistant bacterium (as defined by the study authors) was detected that was not present in the baseline culture.” We also changed the definition accordingly in the abstract (L 36 ff). We hope that the definition of acquisition is now clearer. Our definition of “acquisition of resistance” is agnostic to bacterial species and hence intrinsically resistant species, as the example raised by the reviewer, can be included if they were only detected during the follow-up culture by the studies. Generally, it was not always clear from the studies, which pathogens were screened for and whether the selection of intrinsically resistant bacteria was reported or not. Therefore, we rely on the studies' specifications of resistant and non-resistant without further distinction from our side, i.e. classifying data into intrinsic and non-intrinsic resistance. Overall, the outcome “acquisition of resistance” can be interpreted as a risk assessment for having any resistant bacterium during or after treatment. In contrast, the outcome “emergence of resistance” is more rigorous, demanding the same species to be detected as more resistant during or after treatment.

The information, which antibiotic susceptibility tests were performed in each individual study can be found in the main text in table 1. However, we agree that this information should be better linked and highlighted again in table S1. We therefore now refer to table 1 in the table description of table S1. L134 ff.: “See table 1 in the main text for which antibiotics the antibiotics tested and reported extractable resistance data”. Furthermore, we added the breakpoints for resistant and susceptible classification if specifically stated in the main text of the study. However, we did not do further research into old guidelines, manufactures manuals or study protocols in case the breakpoints are not specifically stated in the main text as the main goal of this table, in our opinion, is to show a justification, why the studies could be considered for a resistance outcome. We therefore decided against further breakpoint investigations for studies, where the breakpoint is not specifically stated in the main text. 

Line 85: "Even though within-patient antibiotic resistance development is rare, it may contribute to the emergence and spread of resistance." 

Depending on the bug-drug combination, there is great variation in the propensity to develop within-patient antibiotic resistance. For example: within-patient development of ciprofloxacin resistance in Pseudomonas is fairly common while within-patient development of methicillin resistance in S. aureus is rare. Based on these differences, large clinical heterogeneity is expected and it is questionable where these studies should be pooled. 

We agree that our formulation neglects differences in prevalence of within-host resistance emergence depending on bug-drug combinations. We changed our statement in L 86 to: “Within-patient antibiotic resistance development, even if rare, may contribute to the emergence and spread of resistance.”

Line 114: "The overall pooled OR for acquisition of resistance comparing a lower number of antibiotics versus a higher one was 1.23 (95% CI 0.68 - 2.25), with substantial heterogeneity between studies (I2=77.4%)" 

What consequential measures did the authors take after determining this high heterogeneity? Did they explore the source of this large heterogeneity? Considering this large heterogeneity, do the authors consider it appropriate to pool these studies?

Thank you for highlighting this lack of clarity. As mentioned above, we now highlight that we performed several subgroup analyses to investigate heterogeneity. (L 116ff): “The overall pooled estimates are based on studies that focus on various clinical conditions/pathogens and compare different antibiotics treatments. To explore the impact of these and other potential sources of heterogeneity on the resistance estimates we performed various subgroup analyses and meta-regression.” Nevertheless, these analyses faced limitations due to the scarcity of evidence and often still showed a high amount of heterogeneity. Given the lack of appropriate evidence, it is hard to identify the source of heterogeneity. The decision to pool all studies was pre-specified in our previously published study protocol (PROSPERO CRD42020187257) and was motivated by the question whether there is a general effect of combination therapy on resistance development or identify factors that explain potential differences of the effect of combination therapy across bug-drug combinations. Therefore, we think that the presentation of the overall pooled estimate is appropriate, as it was predefined, and potential heterogeneity is furthermore explored in the subgroup analyses. 

Reviewer #1 (Recommendations For The Authors): 

I want to congratulate the investigators for the rigorous approach followed and the - in my opinion - correct interpretation of the data and analysis. The disappointing outcome is independent of the quality of the approach used. Yet, the consequences of that outcome are rather limited, and will not be surprising for - at least - some in the field of antibiotic resistance. 

Thank you for your positive and differentiated feedback.

Reviewer #2 (Recommendations For The Authors): 

Line 93: "The screening of the citations of the 41 studies identified one additional eligible study, for a total of 42 studies". 

Why was this study missed in the search strategy? 

What is the definition of "quasi-RCTs"? Why were these included in the analysis? 

Thank you for pointing out this lack of clarity. The additional study, which was found through screening the references of included studies, was not identified with our search strategy as neither the abstract nor database specific identifiers provided any indications that resistance was measured in this study. We added an explanation in the supplementary materials L 792 ff. and refer to this explanation in the main manuscript (L 95). 

Quasi-randomized trials are trials that use allocation methods, which are not considered truly random. We added this specification in L 95. It now reads: “….two quasi-RCTs, where the allocation method used is not truly random” and in L 252 ff: “Studies were classified as quasi-RCTs if the allocation of participants to study arms was not truly random.” For instance, the study Macnab et al. (1994) assigned patients alternately to the treatment arms. Quasi-randomized controlled trials can lead to biases and especially old studies are more likely to have used quasi-random allocation methods. This can also be seen in our study, where the two quasi-randomized controlled trials were published in 1994 and 1997. The bias is considered in the risk of bias assessment and in our conducted sensitivity analysis regarding the impact of risk of bias on our estimates (supplementary information sections 3.0 and 4.2). Furthermore, one of the two previous conducted meta-analyses comparing beta-lactam monotherapy to beta-lactam and aminoglycoside, which assessed resistance development also included quasi-randomized controlled trials Paul et al 2014. Overall, while designing the study, we decided to include quasi-randomized controlled trials to increase statistical power as we expected that limited statistical power might be a concern and decided to assess potential biases in the risk of bias assessment.  

Line 100: "Consequently, most studies did not have the statistical power to detect a large effect on within-patient resistance development (figure 2 B, SI p 14).". 

Small studies actually have more power to detect large effects while smaller power to detect small effects. Please rephrase. 

Thank you for pointing out this lack of clarity. We rephrased the sentence in order to emphasize our point that the studies are underpowered even if we assume in our power analysis a large effect on resistance development between treatment arms. In this context “the small” studies include too few patients to detect a large difference in resistance development. As resistance development is a rare event, generally studies have to include a larger number of patients to estimate the effect of intervention. We rephrased the sentence in L 101ff to: “Consequently, most studies did not have the statistical power to detect differences in within-patient resistance development even if we assume that the effect on resistance development is large between treatment arms.”

Line 108: "... and prophylaxis for blood cancer patients with four studies (10%) respectively.". 

I would suggest using the medical term hematological malignancy patients. 

Thank you for the suggestion, we changed it as suggested to hematological malignancy patients, also accordingly in the figures, and table 1.

Line 117: "Since the results for the two resistance outcomes are comparable, our focus in the following is on the acquisition of resistance". 

The first OR is 1.23 and the second is 0.74, why do you consider these outcomes as comparable? 

Thank you for pointing out our unprecise formulation. Due to the lack of power the exact estimates need to be interpreted with care. Here, we wanted to make the point that qualitatively the results of both outcomes do not differ in the sense that our analysis shows no substantial difference between a higher and a lower number of antibiotics. We rephrased the sentence to be more precise (L 123ff): “The results for the two resistance outcomes are qualitatively comparable in the sense that individual estimates may differ, but show similar absence of evidence to support either the benefit, harm or equivalence of treating with a higher number of antibiotics. Therefore, our …”. More detailed discussion about differences in estimates can be found in the SI, when the estimates of emergence of resistance are presented (e.g. SI section 2.1).

Line 123: "Furthermore, a lower number of antibiotics performed better than a higher number if the compared treatment arms had no antibiotics in common (pooled OR 4.73, 95% CI 2.14 - 10.42; I 2 =37%, SI p 7).". 

How do you explain this? What does this mean? 

We now added a more detailed explanation in the supplement (L 376ff.): “The result that if the treatment arms had no antibiotics in common a lower number of antibiotics performed better than a higher number of antibiotics could be due to different potencies of antibiotics or resistance prevalences. Further, there could be a bias to combine less potent antibiotics or antibiotics with higher resistance prevalence to ensure treatment efficacy, which couldlead to higher chances to detect resistances in the treatment arm with higher number of antibiotics, e.g. by selecting pre-existing resistance due to antibiotic treatment (see also section 6.1.9).” We furthermore already specifically mention this point in the main manuscript and refer then to the detailed explanation in the SI (L134 ff, “which could be due to different potencies or resistance prevalences of antibiotics as discussed in SI (SI section 6.1.10)”)

Overall, we want to point out that these results need to be interpreted with caution as overall the statistical power is limited to confidently estimate the difference in effect of a higher and lower number of antibiotics.

Line 125: ". In contrast, when restricting the analysis to studies with at least one common antibiotic in the treatment arms are pooled there was little evidence of a difference (pooled OR 0.55, 95% CI 0.28 - 1.07". 

The difference was not statistically significant but there does seem to be an indication of a difference, please rephrase. 

We rephrased the sentence to (L135 ff.): “In contrast, when restricting the analysis to studies with at least one common antibiotic in the treatment arms we found no evidence of a difference, only a weak indication that a higher number of antibiotics performs better (pooled OR 0.55, 95% CI 0.28 – 1.07; I2 \=74%, figure 3B).” 

Line 190: "Similarly, today, relevant cohort studies could be analysed collaboratively using various modern statistical methods to address confounding by indication and other biases (66, 67)". 

However, residual confounding by indication is likely. Please also mention the disadvantages of observational studies compared to RCTs. 

We now highlight that causal inference with observational data comes with its own challenges and stress that randomized controlled trials are still considered the gold standard. L 204ff now reads: “However, even with appropriate causal inference methods, residual confounding cannot be excluded when using observational data (67). Therefore, will remain the gold standard to estimate causal relationships.”

Line 230: "Gram-negative bacteria have an outer membrane, which is absent in grampositive bacteria for instance, therefore intrinsic resistance against antibiotics can be observed in gram-negative bacteria (11)". 

Intrinsic resistance is not unique for Gram-negative bacteria but also exists for Grampositive bacteria. 

We agree with the reviewer that intrinsic resistance is not unique to gram-negative bacteria and refined our writing. We additionally added that differences between gram-negative and gram-positive bacteria are not only to be expected due to differing intrinsic resistances but also due to potential differences in the mechanistic interactions of antibiotics, i.e., synergy or antagonism. The paragraph reads now (SI L289): “The gram status of a bacterium may potentially determine how effective an antibiotic, or an antibiotic combination is. Differences between gram-negative and gram-positive bacteria such as distinct bacterial surface organisation can lead to specific intrinsic resistances of gram-negative and grampositive bacteria against antibiotics (55). These structural differences can lead to varying effects of antibiotic combinations between gram-negative and gram-positive bacteria (56).”

eLife assessment

This study provides direct evidence showing that Kv1.8 channels provide the basis for several potassium currents in the two types of sensory hair cells found in the mouse vestibular system. This is an important finding because the nature of the channels underpinning the unusual potassium conductance gK,L in type I hair cells has been under scrutiny for many years. The experimental evidence is compelling and the analysis is rigorous. The study will be of interest to cell and molecular biologists, and vestibular and auditory neuroscientists.

Reviewer #1 (Public Review):

Summary:

In this paper the authors provide a thorough demonstration of the role that one particular type of voltage-gated potassium channel, Kv1.8, plays in a low voltage activated conductance found in type I vestibular hair cells. Along the way, they find that this same channel protein appears to function in type II vestibular hair cells as well, contributing to other macroscopic conductances. Overall, Kv1.8 may provide especially low input resistance and short time constants to facilitate encoding of more rapid head movements in animals that have necks. Combination with other channel proteins, in different ratios, may contribute to the diversified excitability of vestibular hair cells.

Strengths:

The experiments are comprehensive and clearly described, both in text and in the figures. Statistical analyses are provided throughout.

Weaknesses:

None.

Reviewer #2 (Public Review):

The focus of this manuscript was to investigate whether Kv1.8 channels, which have previously been suggested to be expressed in type I hair cells of the mammalian vestibular system, are responsible for the potassium conductance gK,L. This is an important study because gK,L is known to be crucial for the function of type I hair cells, but the channel identity has been a matter of debate for the past 20 years. The authors have addressed this research topic by primarily investigating the electrophysiological properties of the vestibular hair cells from Kv1.8 knockout mice. Interestingly, gK,L was completely abolished in Kv1.8-deficient mice, in agreement with the hypothesis put forward by the authors based on the literature. The surprising observation was that in the absence of Kv1.8 potassium channels, the outward potassium current in type II hair cells was also largely reduced. Type II hair cells express the largely inactivating potassium conductance g,K,A, but not gK,L. The authors concluded that heteromultimerization of non-inactivating Kv1.8 and the inactivating Kv1.4 subunits could be responsible for the inactivating gK,A. Overall, the manuscript is very well written and most of the conclusions are supported by the experimental work. The figures are well described, and the statistical analysis is robust.

Reviewer #3 (Public Review):

Summary:

This paper by Martin et al. describes the contribution of a Kv channel subunit (Kv1.8, KCNA10) to voltage-dependent K+ conductances and membrane properties of type I and type II hair cells of the mouse utricle. Previous work has documented striking differences in K+ conductances between vestibular hair cell types. In particular amniote type I hair cells are known to express a non-typical low-voltage-activated K+ conductance (GK,L) whose molecular identity has been elusive. K+ conductances in hair cells from 3 different mouse genotypes (wildtype, Kv1.8 homozygous knockouts and heterozygotes) are examined here and whole cell patch-clamp recordings indicate a prominent role for Kv1.8 subunits in generating GK,L. Results also interestingly support a role for Kv1.8 subunits in type II hair cell K+ conductances; inactivating conductances in null mice are reduced in type II hair cells from striola and extrastriola regions of the utricle. Kv1.8 is therefore proposed to contribute as a pore-forming subunit for 3 different K+ conductances in vestibular hair cells. The impact of these conductances on membrane responses to current steps is studied in current clamp. Pharmacological experiments use XE991 to block some residual Kv7-mediated current in both hair cell types, but no other pharmacological blockers are used. In addition immunostaining data are presented and raise some questions about Kv7 and Kv1.8 channel localization. Overall, the data present compelling evidence that removal of Kv1.8 produces profound changes in hair cell membrane conductances and sensory capabilities. These changes at hair cell level suggest vestibular function would be compromised and further assessment in terms of balance behavior in the different mice would be interesting.

Strengths:

This study provides strong evidence that Kv1.8 subunits are major contributors to the unusual K+ conductance in type I hair cells of the utricle. It also indicates that Kv1.8 subunits are important for type II hair cell K+ conductances because Kv1.8-/- mice lacked an inactivating A conductance and had reduced delayed rectifier conductance compared to controls. A comprehensive and careful analysis of biophysical profiles is presented of expressed K+ conductances in 3 different mouse genotypes. Voltage-dependent K+ currents are rigorously characterized at a range of different ages and their impact on membrane voltage responses to current input is studied. Some pharmacological experiments are performed in addition to immunostaining to bolster the conclusions from the biophysical studies. The paper has a significant impact in showing the role of Kv1.8 in determining utricular hair cell electrophysiological phenotypes.

Weaknesses:

(1) From previous work it is known that GK,L in type I hair cells has unusual ion permeation and pharmacological properties that differ greatly from type II hair cell conductances. Notably GK,L is highly permeable to Cs+ as well as K+ ions and is slightly permeable to Na+. It is blocked by 4-aminopyridine and divalent cations (Ba2+, Ca2+, Ni2+), enhanced by external K+ and modulated by cyclic GMP. The question arises-if Kv1.8 is a major player and pore-forming subunit in type I and type II cells (and cochlear inner hair cells as shown by Dierich et al. 2020) how are subunits modified to produce channels with very different properties? A role for Kv1.4 channels (gA) is proposed in type II hair cells based on previous findings in bird hair cells. However, hair cell specific partner interactions with Kv1.8 that result in GK,L in type I hair cells and Cs+ impermeable, inactivating currents in type II hair cells remain for the most part unexplored.

(2) Data from patch-clamp and immunocytochemistry experiments are not in close alignment. XE991 (Kv7 channel blocker) decreases remaining K+ conductance in type I and type II hair cells from null mice supporting the presence of Kv7 channels in hair cells (Fig. 7). Also, Holt et al. (2007) previously showed inhibition of GK,L in type I hair cells (but not delayed rectifier conductance in type II hair cells) using a dominant negative construct of Kv7.4 channels. However, immunolabelling indicates Kv7.4 channels on the inner face of calyx terminals adjacent to hair cells (Fig. 5). Some reconciliation of these findings is needed.

(3) A previous paper reported that a vestibular evoked potential was abnormal in Kv1.8-/- mice (Lee et al. 2013) as briefly mentioned (lines 94-95). It would be really interesting to know if any vestibular-associated behaviors and/or hearing loss were observed in the mice populations. If responses are compromised at the sensory hair cell level across different zones, degradation of balance function would be anticipated and should be elucidated.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Line 127. Provide a few more words describing the voltage protocol. To the uninitiated, panels A and B will be difficult to understand. "The large negative step is used to first close all channels, then probe the activation function with a series of depolarizing steps to re-open them and obtain the max conductance from the peak tail current at -36 mV. "

We have revised the text as suggested (revision lines 127 to Line 131): “From a holding potential within the gK,L activation range (here –74 mV), the cell is hyperpolarized to –124 mV, negative to EK and the activation range, producing a large inward current through open gK,L channels that rapidly decays as the channels deactivate. We use the large transient inward current as a hallmark of gK,L. The hyperpolarization closes all channels, and then the activation function is probed with a series of depolarizing steps, obtaining the max conductance from the peak tail current at –44 mV (Fig. 1A).”

Incidentally, why does the peak tail current decay? 

We added this text to the figure legend to explain this: “For steps positive to the midpoint voltage, tail currents are very large. As a result, K+ accumulation in the calyceal cleft reduces driving force on K+, causing currents to decay rapidly, as seen in A (Lim et al., 2011).”

The decay of the peak tail current is a feature of gK,L (large K+ conductance) and the large enclosed synaptic cleft (which concentrates K+ that effluxes from the HC). See Govindaraju et al. (2023) and Lim et al. (2011) for modeling and experiments around this phenomenon.

Line 217-218. For some reason, I stumbled over this wording. Perhaps rearrange as "In type II HCs absence of Kv1.8 significantly increased Rin and tauRC. There was no effect on Vrest because the conductances to which Kv1.8 contributes, gA and gDR activate positive to the resting potential. (so which K conductances establish Vrest???). 

We kept our original wording because we wanted to discuss the baseline (Vrest) before describing responses to current injection.

Vrest is presumably maintained by ATP-dependent Na/K exchangers (ATP1a1), HCN, Kir, and mechanotransduction currents. Repolarization is achieved by delayed rectifier and A-type K+ conductances in type II HCs.

Figure 4, panel C - provides absolute membrane potential for voltage responses. Presumably, these were the most 'ringy' responses. Were they obtained at similar Vm in all cells (i.e., comparisons of Q values in lines 229-230). 

We added the absolute membrane potential scale. Type II HC protocols all started with 0 pA current injection at baseline, so they were at their natural Vrest, which did not differ by genotype or zone. Consistent with Q depending on expression of conductances that activate positive to Vrest, Q did not co-vary with Vrest (Pearson’s correlation coefficient = 0.08, p = 0.47, n= 85).

Lines 254. Staining is non-specific? Rather than non-selective? 

Yes, thanks - Corrected (Line 264).

Figure 6. Do you have a negative control image for Kv1.4 immuno? Is it surprising that this label is all over the cell, but Kv1.8 is restricted to the synaptic pole? 

We don’t have a null-animal control because this immunoreactivity was done in rat. While the cuticular plate staining was most likely nonspecific because we see that with many different antibodies, it’s harder to judge the background staining in the hair cell body layer. After feedback from the reviewers, we decided to pull the KV1.4 immunostaining from the paper because of the lack of null control, high background, and inability to reproduce these results in mouse tissue. In our hands, in mouse tissue, both mouse and rabbit anti-KV1.4 antibodies failed to localize to the hair cell membrane. Further optimization or another method could improve that, but for now the single-cell expression data (McInturff et al., 2018) remain the strongest evidence for KV1.4 expression in murine type II hair cells.

Lines 400-404. Whew, this is pretty cryptic. Expand a bit? 

We simplified this paragraph (revision lines 411-413): “We speculate that gA and gDR(KV1.8) have different subunit composition: gA may include heteromers of KV1.8 with other subunits that confer rapid inactivation, while gDR(KV1.8) may comprise homomeric KV1.8 channels, given that they do not have N-type inactivation .”

Line 428. 'importantly different ion channels'. I think I understand what is meant but perhaps say a bit more. 

Revised (Line 438): “biophysically distinct and functionally different ion channels”.

Random thought. In addition to impacting Rin and TauRC, do you think the more negative Vrest might also provide a selective advantage by increasing the driving force on K entry from endolymph? 

When the calyx is perfectly intact, gK,L is predicted to make Vrest less negative than the values we report in our paper, where we have disturbed the calyx to access the hair cell (–80, Govindaraju et al., 2023, vs. –87 mV, here). By enhancing K+ accumulation in the calyceal cleft, the intact calyx shifts EK—and Vrest—positively (Lim et al., 2011), so the effect on driving force may not be as drastic as what you are thinking.

Reviewer #2 (Recommendations For The Authors):

(1) Introduction: wouldn't the small initial paragraph stating the main conclusion of the study fit better at the end of the background section, instead of at the beginning? 

Thank you for this idea, we have tried that and settled on this direct approach to let people know in advance what the goals of the paper are.

(2) Pg.4: The following sentence is rather confusing "Between P5 and P10, we detected no evidence of a non-gK,L KV1.8-dependent.....". Also, Suppl. Fig 1A seems to show that between P5 and P10 hair cells can display a potassium current having either a hyperpolarised or depolarised Vhalf. Thus, I am not sure I understand the above statement. 

Thank you for pointing out unclear wording. We used the more common “delayed rectifier” term in our revision (Lines 144-147): “Between P5 and P10, some type I HCs have not yet acquired the physiologically defined conductance, gK,L.. N effects of KV1.8 deletion were seen in the delayed rectifier currents of immature type I HCs (Suppl. Fig. 1B), showing that they are not immature forms of the Kv1.8-dependent gK,L channels. ”

(3) For the reduced Cm of hair cells from Kv1.8 knockout mice, could another reason be simply the immature state of the hair cells (i.e. lack of normal growth), rather than less channels in the membrane? 

There were no other signs to suggest immaturity or abnormal growth in KV1.8–/– hair cells or mice. Importantly, type II HCs did not show the same Cm effect.

We further discussed the capacitance effect in lines 160-167: “Cm scales with surface area, but soma sizes were unchanged by deletion of KV1.8 (Suppl. Table 2). Instead, Cm may be higher in KV1.8+/+ cells because of gK,L for two reasons. First, highly expressed trans-membrane proteins (see discussion of gK,L channel density in Chen and Eatock, 2000) can affect membrane thickness (Mitra et al., 2004), which is inversely proportional to specific Cm. Second, gK,L could contaminate estimations of capacitive current, which is calculated from the decay time constant of transient current evoked by small voltage steps outside the operating range of any ion channels. gK,L has such a negative operating range that, even for Vm negative to –90 mV, some gK,L channels are voltage-sensitive and could add to capacitive current.”

(4) Methods: The electrophysiological part states that "For most recordings, we used .....". However, it is not clear what has been used for the other recordings.

Thanks for catching this error, a holdover from an earlier ms. version.  We have deleted “For most recordings” (revision line 466).

Also, please provide the sign for the calculated 4 mV liquid junction potential. 

Done (revision line 476).

Reviewer #3 (Recommendations For The Authors): 

(1) Some of the data in panels in Fig. 1 are hard to match up. The voltage protocols shown in A and B show steps from hyperpolarized values to -71mV (A) and -32 mV (B). However, the value from A doesn't seem to correspond with the activation curve in C.

Thank you for catching this.  We accidentally showed the control I-X curve from a different cell than that in A. We now show the G-V relation for the cell in A.

Also the Vhalf in D for -/- animals is ~-38 mV, which is similar to the most positive step shown in the protocol.

The most positive step in Figure 1B is actually –25 mV. The uneven tick labels might have been confusing, so we re-labeled them to be more conventional.

Were type I cells stepped to more positive potentials to test for the presence of voltage-activated currents at greater depolarizations? This is needed to support the statement on lines 147-148. 

We added “no additional K+ conductance activated up to +40 mV” (revision line 149-150).  Our standard voltage-clamp protocol iterates up to ~+40 mV in KV1.8–/– hair cells, but in Figure 1 we only showed steps up to –25 mV because K+ accumulation in the synaptic cleft with the calyx distorts the current waveform even for the small residual conductances of the knockouts. KV1.8–/– hair cells have a main KV conductance with a Vhalf of ~–38 mV, as shown in Figure 1, and we did not see an additional KV conductance that activated with a more positive Vhalf up to +40 mV.

(2) Line 151 states "While the cells of Kv1.8-/- appeared healthy..." how were epithelia assessed for health? Hair cells arise from support cells and it would be interesting to know if Kv1.8 absence influences supporting cells or neurons. 

We added our criteria for cell health to lines 477-479: “KV1.8–/– hair cells appeared healthy in that cells had resting potentials negative to –50 mV, cells lasted a long time (20-30 minutes) in ruptured patch recordings, membranes were not fragile, and extensive blebbing was not seen.”

Supporting cells were not routinely investigated. We characterized calyx electrical activity (passive membrane properties, voltage-gated currents, firing pattern) and didn’t detect differences between +/+, +/–, and –/– recordings (data not shown). KV1.8 was not detected in neural tissue (Lee et al., 2013). 

(3) Several different K+ channel subtypes were found to contribute to inner hair cell K+ conductances (Dierich et al. 2020) but few additional K+ channel subtypes are considered here in vestibular hair cells. Further comments on calcium-activated conductances (lines 310-317) would be helpful since apamin-sensitive SK conductances are reported in type II hair cells (Poppi et al. 2018) and large iberiotoxin-sensitive BK conductances in type I hair cells (Contini et al. 2020). Were iberiotoxin effects studied at a range of voltages and might calcium-dependent conductances contribute to the enhanced resonance responses shown in Fig. 4? 

We refer you to lines 310-317 in the original ms (lines 322-329 in the revised ms), where we explain possible reasons for not observing IK(Ca) in this study.

(4) Similar to GK,L erg (Kv11) channels show significant Cs+-permeability. Were experiments using Cs+ and/or Kv11 antagonists performed to test for Kv11? 

No. Hurley et al. (2006) used Kv11 antagonists to reveal Kv11 currents in rat utricular type I hair cells with perforated patch, which were also detected in rats with single-cell RT-PCR (Hurley et al. 2006) and in mice with single-cell RNAseq (McInturff et al., 2018).  They likely contribute to hair cell currents, alongside Kv7, Kv1.8, HCN1, and Kir. 

(5) Mechanosensitive ("MET") channels in hair cells are mentioned on lines 234 and 472 (towards the end of the Discussion), but a sentence or two describing the sensory function of hair cells in terms of MET channels and K+ fluxes would help in the Introduction too. 

Following this suggestion we have expanded the introduction with the following lines  (78-87): “Hair cells are known for their large outwardly rectifying K+ conductances, which repolarize membrane voltage following a mechanically evoked perturbation and in some cases contribute to sharp electrical tuning of the hair cell membrane.  Because gK,L is unusually large and unusually negatively activated, it strongly attenuates and speeds up the receptor potentials of type I HCs (Correia et al., 1996; Rüsch and Eatock, 1996b). In addition, gK,L augments a novel non-quantal transmission from type I hair cell to afferent calyx by providing open channels for K+ flow into the synaptic cleft (Contini et al., 2012, 2017, 2020; Govindaraju et al., 2023), increasing the speed and linearity of the transmitted signal (Songer and Eatock, 2013).”

(6) Lines 258-260 state that GKL does not inactivate, but previous literature has documented a slow type of inactivation in mouse crista and utricle type I hair cells (Lim et al. 2011, Rusch and Eatock 1996) which should be considered. 

Lim et al. (2011) concluded that K+ accumulation in the synaptic cleft can explain much of the apparent inactivation of gK,L. In our paper, we were referring to fast, N-type inactivation. We changed that line to be more specific; new revision lines 269-271: “KV1.8, like most KV1 subunits, does not show fast inactivation as a heterologously expressed homomer (Lang et al., 2000; Ranjan et al., 2019; Dierich et al., 2020), nor do the KV1.8-dependent channels in type I HCs, as we show, and in cochlear inner hair cells (Dierich et al., 2020).”

(7) Lines 320-321 Zonal differences in inward rectifier conductances were reported previously in bird hair cells (Masetto and Correia 1997) and should be referenced here.

Zonal differences were reported by Masetto and Correia for type II but not type I avian hair cells, which is why we emphasize that we found a zonal difference in I-H in type I hair cells. We added two citations to direct readers to type II hair cell results (lines 333-334): “The gK,L knockout allowed identification of zonal differences in IH and IKir in type I HCs, previously examined in type II HCs (Masetto and Correia, 1997; Levin and Holt, 2012).”

Also, Horwitz et al. (2011) showed HCN channels in utricles are needed for normal balance function, so please include this reference (see line 171). 

Done (line 184).

(8) Fig 6A. Shows Kv1.4 staining in rat utricle but procedures for rat experiments are not described. These should be added. Also, indicate striola or extrastriola regions (if known). 

We removed KV1.4 immunostaining from the paper, see above.

(9) Table 6, ZD7288 is listed -was this reagent used in experiments to block Gh? If not please omit. 

ZD7288 was used to block gH to produce a clean h-infinity curve in Figure 6, which is described in the legend.

(10) In supplementary Fig. 5A make clear if the currents are from XE991 subtraction. Also, is the G-V data for single cell or multiple cells in B? It appears to be from 1 cell but ages P11-505 are given in legend. 

The G-V curve in B is from XE991 subtraction, and average parameters in the figure caption are for all the KV1.8–/–  striolar type I hair cells where we observed this double Boltzmann tail G-V curve. I added detail to the figure caption to explain this better.

(11) Supplementary Fig. 6A claims a fast activation of inward rectifier K+ channels in type II but not type I cells-not clear what exactly is measured here.

We use “fast inward rectifier” to indicate the inward current that increases within the first 20 ms after hyperpolarization from rest (IKir, characterized in Levin & Holt, 2012) in contrast to HCN channels, which open over ~100 ms. We added panel C to show that the activation of IKir is visible in type II hair cells but not in the knockout type I hair cells that lack gK,L. IKir was a reliable cue to distinguish type I and type II hair cells in the knockout.

For our actual measurements in Fig 6B, we quantified the current flowing after 250 ms at –124 mV because we did not pharmacologically separate IKir and IH.

Could the XE991-sensitive current be activated and contributing?

The XE991-sensitive current could decay (rapidly) at the onset of the hyperpolarizing step, but was not contributing to our measurement of IKir­ and IH, made after 250 ms at –124 mV, at which point any low-voltage-activated (LVA) outward rectifiers have deactivated. Additionally, the LVA XE991-sensitive currents were rare (only detected in some striolar type I hair cells) and when present did not compete with fast IKir, which is only found in type II hair cells.

Also, did the inward rectifier conductances sustain any outward conductance at more depolarized voltage steps? 

For the KV1.8-null mice specifically, we cannot answer the question because we did not use specific blocking agents for inward rectifiers.  However, we expect that there would only be sustained outward IR currents at voltages between EK and ~-60 mV: the foot of IKir’s I-V relation according to published data from mouse utricular hair cells – e.g., Holt and Eatock 1995, Rusch and Eatock 1996, Rusch et al. 1998, Horwitz et al., 2011, etc.  Thus, any such current would be unlikely to contaminate the residual outward rectifiers in Kv1.8-null animals, which activate positive to ~-60 mV. 

(I-HCN is also not a problem, because it could only be outward positive to its reversal potential at ~-40 mV, which is significantly positive to its voltage activation range.)

Reviewer #2 (Public Review):

Summary:

The authors provide evidence that helps resolve long-standing questions about the differential involvement of the frontal and posterior cortex in working memory. They show that whereas the early visual cortex shows stronger decoding of memory content in a memorization task vs a more complex categorization task, the frontal cortex shows stronger decoding during categorization tasks than memorization tasks. They find that task-optimized RNNs trained to reproduce the memorized orientations show some similarities in neural decoding to people. Together, this paper presents interesting evidence for differential responsibilities of brain areas in working memory.

Strengths:

This paper was strong overall. It had a well-designed task, best-practice decoding methods, and careful control analyses. The neural network modelling adds additional insight into the potential computational roles of different regions.

Weaknesses:

While the RNN model matches some of the properties of the task and decoding, its ability to reproduce the detailed findings of the paper was limited. Overall, the RRN model was not as well-motivated as the fMRI analyses.

Author response:

(1) Reviewer 1 suggested that we repeat the analyses in additional ROIs in the prefrontal cortex (PFC). We appreciate this suggestion and believe it will contribute to a comprehensive understanding of the current findings. These results will be included in the revision.

(2) Reviewer 1 suggested that we also examine results in motor-related ROIs to rule out influences from response planning. We would like to note that our experimental design makes it unlikely that response planning would have influenced our results, as participants were unable to plan their motor responses in advance due to randomized response mapping on a trial-by-trial basis. Nevertheless, we agree with the reviewer that showing results from motor-related ROIs is important, and will include these results in the revision.

(3) Reviewer 1 raised a question about the effect size of the results across different ROIs. In our manuscript, we tried to avoid direct comparisons of representational strength across ROIs, by focusing on the differences in representational strength between conditions within the same ROI. Nevertheless, we agree that clarifying this issue is important, which we will address in the revision.

(4) Reviewer 2 raised a concern about the similarity between the RNN and fMRI results. We acknowledge that the complexity of our results makes it challenging to replicate all fMRI findings within a single RNN (e.g., simulating three brain regions in a single network with distinct result patterns). Nonetheless, the current RNNs effectively captured our key fMRI findings, including increased stimulus representation in frontal cortex as well as the tradeoff in category representation with varying levels of flexible control. Reviewer 2 also made several suggestions in tweaking the RNN structure and in choosing alternative analysis methods. We are happy to carry out these points as we think they could potentially increase the alignment between the two modalities.

eLife assessment

This valuable study is a companion to a paper introducing a theoretical framework and methodology for identifying Cancer Driving Nucleotides (CDNs). While the evidence that recurrent SNVs or CDNs are common in true cancer driver genes is solid, the evidence that many more undiscovered cancer driver mutations will have CDNs, and that this approach could identify these undiscovered driver genes with about 100,000 samples, is limited.

Reviewer #1 (Public Review):

The study investigates Cancer Driving Nucleotides (CDNs) using the TCGA database, finding that these recurring point mutations could greatly enhance our understanding of cancer genomics and improve personalized treatment strategies. Despite identifying 50-150 CDNs per cancer type, the research reveals that a significant number remain undiscovered, limiting current therapeutic applications, and underscoring the need for further larger-scale research.

Strengths:

The study provides a detailed examination of cancer-driving mutations at the nucleotide level, offering a more precise understanding than traditional gene-level analyses. The authors found a significant number of CDNs remain undiscovered, with only 0-2 identified per patient out of an expected 5-8, indicating that many important mutations are still missing. The study indicated that identifying more CDNs could potentially significantly impact the development of personalized cancer therapies, improving patient outcomes.

Weaknesses:

The study is constrained by relatively small sample sizes for each cancer type, which reduces the statistical power and robustness of the findings. ICGC and other large-scale WGS datasets are publicly available but were not included in this study.

To be able to identify rare driver mutations, more samples are needed to improve the statistical power, which is well-known in cancer research.

The challenges in direct functional testing of CDNs due to the complexity of tumor evolution and unknown mutation combinations limit the practical applicability of the findings.

The QC of the TCGA data was not very strict, i.e, "patients with more than 3000 coding region point mutations were filtered out as potential hypermutator phenotypes", it would be better to remove patients beyond +/- 3*S.D from the mean number of mutations for each cancer type. Given some point mutations with >3 hits in the TCGA dataset, they were just false positive mutation callings, particularly in the large repeat regions in the human genome.

The codes for the statistical calculation (i.e., calculation of Ai_e, et al) are not publicly available, which makes the findings hard to be replicated.

Reviewer #2 (Public Review):

Summary:

The study proposes that many cancer driver mutations are not yet identified but could be identified if they harbor recurrent SNVs. The paper leverages the analysis from Paper #1 that used quantitative analysis to demonstrate that SNVs or CDNs seen 3 or more times are more likely to occur due to selection (ie a driver mutation) than they are to occur by chance or random mutation.

Strengths:

Empirically, mutation frequency is an excellent marker of a driver gene because canonical driver mutations typically have recurrent SNVs. Using the TCGA database, the paper illustrates that CDNs can identify canonical driver mutations (Figure 3) and that most CDNs are likely to disrupt protein function (Figure 2). In addition, CDNs can be shared between cancer types (Figure 4).

Weaknesses:

Driver alteration validation is difficult, with disagreements on what defines a driver mutation, and how many driver mutations are present in a cancer. The value proposed by the authors is that the identification of all driver genes can facilitate the design of patient-specific targeting therapies, but most targeted therapies are already directed towards known driver genes. There is an incomplete discussion of oncogenes (where activating mutations tend to target a single amino acid or repeat) and tumor suppressor genes (where inactivating mutations may be more spread across the gene). Other alterations (epigenetic, indels, translocations, CNVs) would be missed by this type of analysis.

The method could be more valuable when applied to the noncoding genome, where driver mutations in promoters or enhancers are relatively rare, or as yet to be discovered. Increasingly more cancers have had whole genome sequencing. Compared to WES, criteria for driver mutations in noncoding regions are less clear, and this method could potentially provide new noncoding driver CDNs. Observing the same mutation in more than one cancer specimen is empirically unusual, and the authors provide a solid quantitative analysis that indicates many recurrent mutations are likely to be cancer-driver mutations.

Author response:

We are grateful to the reviewers and editors for their insightful comments. All recognized that, while mutation recurrences have been used for inferring cancer drivers, our approach has the rigor of quantitative analysis. We would like to add that, without rigorously ruling out mutational hotspots, most CDNs have not been accepted as driver mutations.

This paper develops the theory stating that (i) recurrent point mutations are true Cancer Driving Nucleotides (CDNs); and (ii) non-recurrent mutations are unlikely to be CDNs. The reviewers question that, with the theory, we still have not discovered new driving mutations. This is done in the companion paper. Table 3 shows that, averaged across cancer types, the conventional method would identify 45 CDGs while the CDN method tallies 258 CDGs. The power of the CDN method in identifying new driver genes is evident.

The second question is "By this theory, will we be able discover most CDNs when the sample size increases from ~ 1000 to 10,000?" This is a question of forecast and can be partially answered using GENIE data. Fig. 7 of this study shows that, when n increases from ~ 1000 to ~ 9,000, the numbers of discovered CDNs increase by 3 – 5 fold, most of which come from the two-hit class, as expected.

Fig. 7 also addresses the queries whether we have used datasets other than TCGA. We indeed have used all public data, including GENIE, ICGC and other integrated resources such as COSMIC. For the main study, we rely on TCGA because it is unbiased for estimating the probability of CDN occurrences. In many datasets, the numerators are given but the denominators are not (the number of patients with the mutation / the total number of patients surveyed). 

The third question is about mutation recurrences among cancer types. As stated by one reviewer, "different cancer types have unique mutational landscapes". While this is true when the analysis is done at the whole-gene level, one gets a different picture at the nucleotide level where the resolution is much higher. The pan-cancer trend of point mutations is evident in Fig. 4 of the companion paper.

Again, we heartily appreciate the criticisms and suggestions of the reviewers and editors!

Author response:

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

Reviewer #1 (Public Review):

[...] Overall the manuscript is well written, and the successful generation of the new endogenous Cac tags (Td-Tomato, Halo) and CaBeta, stj, and stolid genes with V5 tags will be powerful reagents for the field to enable new studies on calcium channels in synaptic structure, function, and plasticity. There are also some interesting, though not entirely unexpected, findings regarding how Brp and homeostatic plasticity modulate calcium channel abundance. However, a major concern is that the conclusions about how "molecular and organization diversity generate functional synaptic heterogeneity" are not really supported by the data presented in this study. In particular, the key fact that frames this study is that Cac levels are similar at Ib and Is active zones, but that Pr is higher at Is over Ib (which was previously known). While Pr can be influenced by myriad processes, the authors should have first assessed presynaptic calcium influx - if they had, they would have better framed the key questions in this study. As the authors reference from previous studies, calcium influx is at least two-fold higher per active zone at Is over Ib, and the authors likely know that this difference is more than sufficient to explain the difference in Pr at Is over Ib. Hence, there is no reason to invoke differences in "molecular and organization diversity" to explain the difference in Pr, and the authors offer no data to support that the differences in active zone structure at Is vs Ib are necessary for the differences in Pr. Indeed, the real question the authors should have investigated is why there are such differences in presynaptic calcium influx at Is over Ib despite having similar levels/abundance of Cac. This seems the real question, and is all that is needed to explain the Pr differences shown in Fig. 1. The other changes in active zone structure and organization at Is vs Ib may very well contribute to additional differences in Pr, but the authors have not shown this in the present study, and rely on other studies (such as calcium-SV coupling at Is vs Ib) to support an argument that is not necessitated by their data. At the end of this manuscript, the authors have found an interesting possibility that Stj levels are reduced at Is vs Ib, that might perhaps contribute to the difference in calcium influx. However, at present this remains speculative.

Overall, the authors have generated powerful reagents for the field to study calcium channels and how they are regulated, but draw conclusions about active zone structure and organization contributing to functional heterogeneity that are not strongly supported by the data presented.

Reviewer 1 raises an interesting question that we agree will form the basis of important studies. Here, we set out to address a different question, which we will work to better frame. While we and others had previously found a strong correlation between calcium channel abundance and synaptic release probability (Pr (Akbergenova et al., 2018; Gratz et al., 2019; Holderith et al., 2012; Nakamura et al., 2015; Sheng et al., 2012)), more recent studies found that calcium channel abundance does not necessarily predict synaptic strength (Aldahabi et al., 2022; Rebola et al., 2019). Our study explores this paradox and presents findings that provide an explanation: calcium channel abundance predicts Pr among individual synapses of either low-Pr type-Ib or high-Pr type-Is inputs where modulating channel number tunes synaptic strength, but does not predict Pr between the two inputs, indicating an inputspecific role for calcium channel abundance in promoting synaptic strength. Thus, we propose that calcium channel abundance predictably modulates synaptic strength among individual synapses of a single input or synapse subtype, which share similar molecular and spatial organization, but not between distinct inputs where the underlying organization of active zones differs. Consistently, in the mouse, calcium channel abundance correlates strongly with release probability specifically when assessed among homogeneous populations of connections (Aldahabi et al., 2022; Holderith et al., 2012; Nakamura et al., 2015; Rebola et al., 2019; Sheng et al., 2012).

As Reviewer 1 notes, the two-fold difference in calcium influx at type-Is synapses is certainly an important difference underlying three-fold higher Pr. However, growing evidence indicates that calcium influx alone, like calcium channel abundance, does not reliably predict synaptic strength between inputs. For example, Rebola et al. (2019) compared cerebellar synapses formed by granule and stellate cells and found that lower Pr granule synapses exhibit both higher calcium channel abundance and calcium influx. In another example, Aldahabi et al. (2023) demonstrate that even when calcium influx is greater at high-Pr synapses, it does not necessarily explain differences in synaptic strength between inputs. Studying excitatory hippocampal CA1 synapses onto distinct interneuronal targets, they found that raising calcium entry at low-Pr inputs to high-Pr synapse levels is not sufficient to increase synaptic strength to high-Pr synapse levels. Similarly, at the Drosophila NMJ, the finding that type-Ib synapses exhibit loose calcium channel-synaptic vesicle coupling whereas type-Is synapses exhibit tight coupling suggests factors beyond calcium influx also contribute to differences in Pr between the two inputs (He et al., 2023). Consistently, a two-fold increase in external calcium does not induce a three-fold increase in release at low-Pr type-Ib synapses (He et al., 2023). Thus, upon finding that calcium channel abundance is similar at type-Ib and -Is synapses, we focused on identifying differences beyond calcium channel abundance and calcium influx that might contribute their distinct synaptic strengths. We agree that these studies, ours included, cannot definitively determine the contribution of identified organizational differences to distinct release probabilities because it is not currently possible to specifically alter subsynaptic organization, and will ensure that our language is tempered accordingly. However, in addition to the studies cited above and our findings, recent work demonstrating that homeostatic potentiation of neurotransmitter release is accompanied by greater spatial compaction of multiple active zone proteins (Dannhauser et al., 2022; Mrestani et al., 2021) and decreased calcium channel mobility (Ghelani et al., 2023) provide support for the interpretation that subsynaptic organization is a key parameter for modulating Pr.

Reviewer #2 (Public Review):

The authors aim to investigate how voltage-gated calcium channel number, organization, and subunit composition lead to changes in synaptic activity at tonic and phasic motor neuron terminals, or type Is and Ib motor neurons in Drosophila. These neuron subtypes generate widely different physiological outputs, and many investigations have sought to understand the molecular underpinnings responsible for these differences. Additionally, these authors explore not only static differences that exist during the third-instar larval stage of development but also use a pharmacological approach to induce homeostatic plasticity to explore how these neuronal subtypes dynamically change the structural composition and organization of key synaptic proteins contributing to physiological plasticity. The Drosophila neuromuscular junction (NMJ) is glutamatergic, the main excitatory neurotransmitter in the human brain, so these findings not only expand our understanding of the molecular and physiological mechanisms responsible for differences in motor neuron subtype activity but also contribute to our understanding of how the human brain and nervous system functions.

The authors employ state-of-the-art tools and techniques such as single-molecule localization microscopy 3D STORM and create several novel transgenic animals using CRISPR to expand the molecular tools available for exploration of synaptic biology that will be of wide interest to the field. Additionally, the authors use a robust set of experimental approaches from active zone level resolution functional imaging from live preparations to electrophysiology and immunohistochemical analyses to explore and test their hypotheses. All data appear to be robustly acquired and analyzed using appropriate methodology. The authors make important advancements to our understanding of how the different motor neuron subtypes, phasic and tonic-like, exhibit widely varying electrical output despite the neuromuscular junctions having similar ultrastructural composition in the proteins of interest, voltage gated calcium channel cacophony (cac) and the scaffold protein Bruchpilot (brp). The authors reveal the ratio of brp:cac appears to be a critical determinant of release probability (Pr), and in particular, the packing density of VGCCs and availability of brp. Importantly, the authors demonstrate a brp-dependent increase in VGCC density following acute philanthotoxin perfusion (glutamate receptor inhibitor). This VGCC increase appears to be largely responsible for the presynaptic homeostatic plasticity (PHP) observable at the Drosophila NMJ. Lastly, the authors created several novel CRISPRtagged transgenic lines to visualize the spatial localization of VGCC subunits in Drosophila. Two of these lines, CaBV5-C and stjV5-N, express in motor neurons and in the nervous system, localize at the NMJ, and most strikingly, strongly correlate with Pr at tonic and phasic-like terminals.

(1) The few limitations in this study could be addressed with some commentary, a few minor follow-up analyses, or experiments. The authors use a postsynaptically expressed calcium indicator (mhcGal4>UAS -GCaMP) to calculate Pr, yet do not explore the contribution that glutamate receptors, or other postsynaptic contributors (e.g. components of the postsynaptic density, PSD) may contribute. A previous publication exploring tonic vs phasic-like activity at the drosophila NMJ revealed a dynamic role for GluRII (Aponte-Santiago et al, 2020). Could the speed of GluR accumulation account for differences between neuron subtypes?

We did observe that GCaMP signals are higher at type Is synapses, where synapses tend to form later but GluRs accumulate more rapidly upon innervation (Aponte-Santiago et al., 2020). However, because we are using our GCaMP indicator as a plus/minus readout of synaptic vesicle release at mature synapses, we do not expect differences in GluR accumulation to have a significant effect on our measures. Consistently, the difference in Pr we observe between type-Ib and -Is inputs (Fig. 1C) is similar to that previously reported (He et al., 2023; Lu et al., 2016; Newman et al., 2022).

(2) The observation that calcium channel density and brp:cac ratio as a critical determinant of Pr is an important one. However, it is surprising that this was not observed in previous investigations of cac intensity (of which there are many). Is this purely a technical limitation of other investigations, or are other possibilities feasible? Additionally, regarding VGCC-SV coupling, the authors conclude that this packing density increases their proximity to SVs and contributes to the steeper relationship between VGCCs and Pr at phasic type Is. Is it possible that brp or other AZ components could account for these differences. The authors possess the tools to address this directly by labeling vesicles with JanellaFluor646; a stronger signal should be present at Is boutons. Additionally, many different studies have used transmission electron microscopy to explore SVs location to AZs (t-bars) at the Drosophila NMJ.

To date, the molecular underpinnings of heterogeneity in synaptic strength have primarily been investigated among individual type-Ib synapses. However, a recent study investigating differences between type-Ib and -Is synapses also found that the Cac:Brp ratio is higher at type-Is synapses (He et al., 2023).

At this point, we do not know which active zone components are responsible for the organizational (Figs. 1, 2) and coupling (now demonstrated by He et al., 2023) differences between type-Ib and -Is synapses or what establishes the differences in active zone protein levels we observe (Figs. 3,6), although Brp likely plays a local role. We find that Brp is required for dynamically regulating calcium channel levels during homeostatic plasticity and plays distinct roles at type-Ib and -Is synapses (Figs. 3, 4). Brp regulates a number of proteins critical for the distribution of docked synaptic vesicles near T bars of type Ib active zones, including Unc13 (Bohme et al., 2016). Extending these studies to type-Is synapses will be of great interest.

(3) In reference to the contradictory observations that VGCC intensity does not always correlate with, or determine Pr. Previous investigations have also observed other AZ proteins or interactors (e.g. synaptotagmin mutants) critically control release, even when the correlation between cac and release remains constant while Pr dramatically precipitates.

This is an important point as a number of molecular and organizational differences between high- and low-Pr synapses certainly contribute to baseline functional differences. The other proteins we (Figs. 3,6) and others (Dannhauser et al., 2022; Ehmann et al., 2014; He et al., 2023; Jetti et al., 2023; Mrestani et al., 2021; Newman et al., 2022) have investigated are less abundant and/or more densely organized at type-Is synapses. Investigating additional active zone proteins, including synaptic proteins, and determining how these factors combine to yield increased synaptic strength are important next steps.

(4) To confirm the observations that lower brp levels results in a significantly higher cac:brp ratio at phasic-like synapses by organizing VGCCs; this argument could be made stronger by analyzing their existing data. By selecting a population of AZs in Ib boutons that endogenously express normal cac and lower brp levels, the Pr from these should be higher than those from within that population, but comparable to Is Pr. I believe the authors should also be able to correlate the cac:brp ratio with Pr from their data set generally; to determine if a strong correlation exists beyond their observation for cac correlation.

We do not have simultaneous measures of Pr and Cac and Brp abundance. However, our findings suggest that distinct Cac:Brp ratios at type Ib and Is inputs reflect underlying organizational differences that contribute to distinct release probabilities between the two synaptic subtypes. In contrast, within either synaptic subtype, release probability is positively correlated with both Cac and Brp levels. Thus, the mechanisms driving functional differences between synaptic subtypes are distinct from those driving functional heterogeneity within a subtype, so we do not expect Cac:Brp ratio to correlate with Pr among individual type-Ib synapses. We will work to clarify this point in the revised text.

(5) For the philanthotoxin induced changes in cac and brp localization underlying PHP, why do the authors not show cac accumulation after PhTx on live dissected preparations (i.e. in real time)? This also be an excellent opportunity to validate their brp:cac theory. Do the authors observe a dynamic change in brp:cac after 1, or 5 minutes; do Is boutons potentiate stronger due to proportional increases in cac and brp? Also regarding PhTx-induced PHP, their observations that stj and α2δ-3 are more abundant at Is synapses, suggests that they may also play a role in PhTx induced changes in cac. If either/both are overexpressed during PhTx, brp should increase while cac remains constant. These accessory proteins may determine cac incorporation at AZs.

As we have previously followed Cac accumulation in live dissected preparations and found that levels increase proportionally across individual synapses (Gratz et al., 2019), we did not attempt to repeat these challenging experiments at smaller type-Is synapses. We will reanalyze our data to investigate Cac:Brp ratio at individual active zones post PhTx. However, as noted above, we do not expect changes in the Cac:Brp ratio to correlate with Pr among individual synapses of single inputs as this measure reflects organization differences between inputs and PhTx induces an increase in the abundance of both proteins at both inputs.

Determining the effect of PhTx on Stj levels at type-Ib and -Is active zones is an excellent idea and might provide insight into how lower Stj levels correlate with higher Pr at type-Is synapses. While prior studies have demonstrated critical roles for Stj in regulating Cac accumulation during development and in promoting presynaptic homeostatic potentiation (Cunningham et al., 2022; Dickman et al., 2008; Kurshan et al., 2009; Ly et al., 2008; Wang et al., 2016), its regulation during PHP has not been investigated.

Taken together this study generates important data-driven, conceptional, and theoretical advancements in our understanding of the molecular underpinnings of different motor neurons, and our understanding of synaptic biology generally. The data are robust, thoroughly analyzed, appropriately depicted. This study not only generates novel findings but also generated novel molecular tools which will aid future investigations and investigators progress in this field.

References

Akbergenova, Y., K.L. Cunningham, Y.V. Zhang, S. Weiss, and J.T. Littleton. 2018. Characterization of developmental and molecular factors underlying release heterogeneity at Drosophila synapses. eLife. 7.

Aldahabi, M., F. Balint, N. Holderith, A. Lorincz, M. Reva, and Z. Nusser. 2022. Different priming states of synaptic vesicles underlie distinct release probabilities at hippocampal excitatory synapses. Neuron. 110:4144-4161 e4147.

Aponte-Santiago, N.A., K.G. Ormerod, Y. Akbergenova, and J.T. Littleton. 2020. Synaptic Plasticity Induced by Differential Manipulation of Tonic and Phasic Motoneurons in Drosophila. The Journal of neuroscience : the official journal of the Society for Neuroscience. 40:6270-6288.

Bohme, M.A., C. Beis, S. Reddy-Alla, E. Reynolds, M.M. Mampell, A.T. Grasskamp, J. Lutzkendorf, D.D. Bergeron, J.H. Driller, H. Babikir, F. Gottfert, I.M. Robinson, C.J. O'Kane, S.W. Hell, M.C. Wahl, U. Stelzl, B. Loll, A.M. Walter, and S.J. Sigrist. 2016. Active zone scaffolds differentially accumulate Unc13 isoforms to tune Ca(2+) channel-vesicle coupling. Nature neuroscience. 19:1311-1320.

Cunningham, K.L., C.W. Sauvola, S. Tavana, and J.T. Littleton. 2022. Regulation of presynaptic Ca(2+) channel abundance at active zones through a balance of delivery and turnover. Elife. 11.

Dannhauser, S., A. Mrestani, F. Gundelach, M. Pauli, F. Komma, P. Kollmannsberger, M. Sauer, M. Heckmann, and M.M. Paul. 2022. Endogenous tagging of Unc-13 reveals nanoscale reorganization at active zones during presynaptic homeostatic potentiation. Front Cell Neurosci. 16:1074304.

Dickman, D.K., P.T. Kurshan, and T.L. Schwarz. 2008. Mutations in a Drosophila alpha2delta voltage gated calcium channel subunit reveal a crucial synaptic function. The Journal of neuroscience : the official journal of the Society for Neuroscience. 28:31-38.

Ehmann, N., S. Van De Linde, A. Alon, D. Ljaschenko, X.Z. Keung, T. Holm, A. Rings, A. Diantonio, S. Hallermann, U. Ashery, M. Heckmann, M. Sauer, and R.J. Kittel. 2014. Quantitative super-resolution imaging of Bruchpilot distinguishes active zone

states. Nature Communications. 5.

Ghelani, T., M. Escher, U. Thomas, K. Esch, J. Lützkendorf, H. Depner, M. Maglione, P. Parutto, S. Gratz, T. Matkovic-Rachid, S. Ryglewski, A.M. Walter, D. Holcman, K. O‘Connor Giles, M. Heine, and S.J. Sigrist. 2023. Interactive nanocluster compaction of the ELKS scaffold and Cacophony Ca²⁺ channels drives sustained active zone potentiation. Science Advances. 9:eade7804.

Gratz, S.J., P. Goel, J.J. Bruckner, R.X. Hernandez, K. Khateeb, G.T. Macleod, D. Dickman, and K.M. O'Connor-Giles. 2019. Endogenous tagging reveals differential regulation of Ca²⁺ channels at single AZs during presynaptic homeostatic potentiation and depression. The Journal of Neuroscience:3068-3018.

He, K., Y. Han, X. Li, R.X. Hernandez, D.V. Riboul, T. Feghhi, K.A. Justs, O. Mahneva, S. Perry, G.T. Macleod, and D. Dickman. 2023. Physiologic and Nanoscale Distinctions Define Glutamatergic Synapses in Tonic vs Phasic Neurons. The Journal of neuroscience : the official journal of the Society for Neuroscience. 43:4598-4611.

Holderith, N., A. Lorincz, G. Katona, B. Rózsa, A. Kulik, M. Watanabe, and Z. Nusser. 2012. Release probability of hippocampal glutamatergic terminals scales with the size of the active zone. Nature neuroscience. 15:988-997.

Jetti, S.K., A.B. Crane, Y. Akbergenova, N.A. Aponte-Santiago, K.L. Cunningham, C.A. Whittaker, and J.T. Littleton. 2023. Molecular Logic of Synaptic Diversity Between Drosophila Tonic and Phasic Motoneurons. bioRxiv:2023.2001.2017.524447.

Kurshan, P.T., A. Oztan, and T.L. Schwarz. 2009. Presynaptic alpha2delta-3 is required for synaptic morphogenesis independent of its Ca2+-channel functions. Nature neuroscience. 12:1415-1423.

Lu, Z., A.K. Chouhan, J.A. Borycz, Z. Lu, A.J. Rossano, K.L. Brain, Y. Zhou, I.A. Meinertzhagen, and G.T. Macleod. 2016. High-Probability Neurotransmitter Release Sites Represent an Energy-Efficient Design. Current biology : CB. 26:2562-2571.

Ly , C.V., C.-K. Yao , P. Verstreken , T. Ohyama , and H.J. Bellen 2008. straightjacket is required for the synaptic stabilization of cacophony, a voltage-gated calcium channel α1 subunit. Journal of Cell Biology. 181:157-170.

Mrestani, A., M. Pauli, P. Kollmannsberger, F. Repp, R.J. Kittel, J. Eilers, S. Doose, M. Sauer, A.-L. Sirén, M. Heckmann, and M.M. Paul. 2021. Active zone compaction correlates with presynaptic homeostatic potentiation. Cell Reports. 37:109770.

Nakamura, Y., H. Harada, N. Kamasawa, K. Matsui, Jason S. Rothman, R. Shigemoto, R.A. Silver, David A. DiGregorio, and T. Takahashi. 2015. Nanoscale Distribution of Presynaptic Ca2+ Channels and Its Impact on Vesicular Release during Development. Neuron. 85:145-158.

Newman, Z.L., D. Bakshinskaya, R. Schultz, S.J. Kenny, S. Moon, K. Aghi, C. Stanley, N. Marnani, R. Li, J. Bleier, K. Xu, and E.Y. Isacoff. 2022. Determinants of synapse diversity revealed by superresolution quantal transmission and active zone imaging. Nature Communications. 13:229.

Rebola, N., M. Reva, T. Kirizs, M. Szoboszlay, A. Lőrincz, G. Moneron, Z. Nusser, and D.A. Digregorio. 2019. Distinct Nanoscale Calcium Channel and Synaptic Vesicle Topographies Contribute to the Diversity of Synaptic Function. Neuron. 104:693-710.e699.

Sheng, J., L. He, H. Zheng, L. Xue, F. Luo, W. Shin, T. Sun, T. Kuner, D.T. Yue, and L.-G. Wu. 2012. Calcium-channel number critically influences synaptic strength and plasticity at the active zone. Nature neuroscience. 15:998-1006.

Wang, T., R.T. Jones, J.M. Whippen, and G.W. Davis. 2016. alpha2delta-3 Is Required for Rapid Transsynaptic Homeostatic Signaling. Cell Rep. 16:2875-2888.

Reviewer #1 (Recommendations For The Authors): 

Major points: 

(1) A central question regarding VGCC differences at Is vs Ib active zones is why is calcium influx higher at Is active zones compared to Ib. Ideally, the authors would have started this study by showing correlations between Cac abundance, presynaptic calcium influx, and Pr at Is vs Ib active zones. If they had, they would likely find that Cac abundance scales with calcium influx and Pr within Is vs Ib, but that calcium influx is over two-fold enhanced at Is over Ib when normalized to the same Cac abundance. This is more than sufficient to explain the Pr differences, so the rest of the study should have focused on revealing why influx is different at Is over Ib despite an apparently similar level of Cac abundance. Then the examination of CaBeta, Stj, etc could have been used to help explain this conundrum. 

A lesson might be gleaned in how to structure this narrative from the Rebola 2019 study, which the authors cite and discuss at length. Similar to the current study, that paper started with two synapses ("strong" vs "weak") and sought to explain why they were so different in synaptic strength. First, they examined presynaptic calcium influx, and surprisingly found that the strong synapse had reduced calcium influx compared to the weak. Then the rest of the paper sought to explain why synaptic strength (Pr) was higher at the strong synapse despite reduced calcium influx. The authors do not use this logical flow and narrative in the present study, despite the focus being on how Cav2 channels contribute to strong vs weak synapses - and the primary function of Cav2 channels is to pass calcium at active zones to drive vesicle fusion. 

Although the authors did not show that presynaptic calcium influx is higher at Is vs Ib active zones in the current manuscript, other studies have previously established that calcium influx is two-fold higher at Is active zones vs Ib (as the authors cite). Rather than focusing so much on Pr at Is vs Ib active zones, which as the authors know can be influenced by myriad differences, it seems the more relevant parameter to study is simply to address presynaptic calcium influx at Is vs Ib, which is the primary function of Cac. Put more simply, if Cac levels are the same at Is vs Ib active zones, why is calcium influx at least two-fold higher at Is? 

It would therefore seem crucial for the authors to determine presynaptic calcium influx levels (ideally at individual AZs) to really understand how Cac intensity levels correlate with calcium influx. The authors instead map Pr at individual AZs, but as the authors know there are many variables that influence whether a SV releases in addition to calcium influx. There are a number of options for this kind of imaging in Drosophila, including genetically encoded calcium indicators targeted to active zones. But since several studies have previously established that influx is higher at Is active zones over Ib, this may not be necessary. That being said, there is a lot of value in quantitatively analyzing Cac/Stj/CaBeta abundance, calcium influx, and Pr together at individual active zones.

We appreciate the perspective that we could have focused on why Ca2+ influx is 2x greater at type Is active zones, which we agree is an important and interesting question. However, growing evidence indicates that Ca2+ influx alone, like Ca2+ channel abundance, does not reliably predict synaptic strength between inputs. So, here we focused instead on how other differences between synapses influence Pr and contribute to synaptic heterogeneity between and/or among synapses formed by strong and weak inputs. We have changed our title and framing to better reflect this focus. 

As Reviewer 1 notes, Rebola et al. (2019) found that lower Pr granule synapses exhibit higher Ca2+ influx (and Ca2+ channel abundance). In another example, Aldahabi et al. (2022) demonstrated that even when Ca2+ influx is greater at high-Pr synapses, it does not necessarily explain differences in synaptic strength as raising Ca2+ entry at low-Pr synapses to high-Pr synapse levels was not sufficient to increase synaptic strength to high-Pr input levels. Similar findings have been reported at tonic and phasic synapses of the Crayfish NMJ (Msghina, 1999).

Several lines of evidence argue that factors beyond Ca2+ influx also play important roles in establishing distinct release properties at the Drosophila NMJ. A recent study using using a botulinum transgene to isolate type Ib and Is synapses for electrophysiological analysis found that increasing external [Ca2+] from physiological levels (1.8 mM) to 3 mM or even 6 mM does not result in a 3-fold increase in EPSCs or quantal content at type Ib synapses despite the prediction that the increase would be even greater given the power dependence of release on between Ca2+ concentration (He et al., 2023). The authors further found that type Ib synapses are more sensitive than type Is synapses to the slow Ca2+ chelator EGTA, indicating looser Ca2+ channel-SV coupling. 

Consistently, we find that although VGCC levels are similar at the two inputs, their density is greater at type Is active zones (Figs. 1 and 2). Our findings also reveal additional molecular differences that may contribute to the observed differences in neurotransmitter release properties between the two inputs, including lower levels of the active zone protein Brp (Fig 3) and the auxiliary subunit α2δ-3/Stj (Fig. 6) at high Pr type Is inputs. In contrast, levels of each of these proteins positively correlate with synaptic strength among active zones of a single input, whether low- or high-Pr (Figs. 1, 3, 6). Similarly, levels of each of these proteins increase during homeostatic potentiation of neurotransmitter release (Figs. 4 and 7). Thus, we propose that two broad mechanisms contribute to synaptic diversity in the nervous system: (1) spatial organization and relative molecular content establish distinct average basal release probabilities that differ between inputs and (2) among individual synapses of distinct inputs, coordinated modulation of Ca2+ channel and active zone protein abundance independently tunes Pr. These intersecting mechanisms provide a framework for understanding the extensive and dynamic synaptic diversity observed across nervous systems.

(2) In addition to key points made above, it seems the authors should at least consider (if not experimentally test) what other differences might contribute to the higher calcium influx at Is over Ib:  

- Distinct splice isoforms of Cac (and/or Stj/Cabeta): The recent RNAseq analysis of gene expression at Is vs Ib motor neurons from Troy Littleton's group may inform this consideration? 

- Stj reduction at Is: Do channel studies in heterologous systems give any insight into VGCC channel function with and without a2d-3? Do Cav2 channels without a2d pass more calcium? This would then offer an obvious solution to the key conundrum underlying this study. 

These are excellent questions that we are actively pursuing. While there is no evidence of differentially expressed splice isoforms of Stj or Ca-β in the recent RNA-seq data from Jetti et al., 2023, subtle changes in Cac isoform usage were observed that may contribute to differences in Ca2+ influx. In heterologous systems, α2δ expression generally increases Ca2+ channel membrane insertion and  Ca2+ currents. However, in vivo α2δ’s can also mediate extracellular interactions that may modulate channel function. We address these points in greater detail in the revised discussion.  

(3) Assess Stj and CaBeta levels at AZs after PhTx: The successful generation of endogenously tagged Stj and CaBeta enables some relatively easy experiments that would be of interest, similar to what the authors present for Cac. Does Brp similarly control Stj and CaBeta at Is vs Ib compared to what they show for Cac? In addition, does homeostatic plasticity similarly change Stj and CaBeta at Is vs Ib compared to what the authors have shown for Cac? i.e., do they both similarly increase in intensity, by the same amount, as Cac? 

We agree and have included an analysis of α2δ-3/Stj levels following PhTx exposure (Fig. 7A-C). We have also investigated the regulation of Stj during chronic presynaptic homeostatic potentiation (Fig. 7D-F). In both cases, StjV5-N levels significantly increase at type Ib and Is active zones, consistent with our finding that among AZs of either type Ib or Is inputs, Stj levels correlate with Cac abundance and, thus, Pr. Together with our and others’ findings, this suggests that coordinated increases Ca2+ channel, auxiliary subunit,  and active zone protein abundance positively tunes synaptic strength at diverse synaptic subtypes.

Minor points: 

(1) Including line numbers would make reviewing/commenting easier. 

We apologize for this oversight and have added line numbers to the revised manuscript.

(2) Fig. 2I: It is not apparent what the mean cluster density is between Ib vs Is (as it is in Fig. 2F-H graphs). The mean and error bars should be included in 2I as it is in 2G. Same with Fig. 3C. 

Thank you for pointing this out. We have added error bars to the paired analysis in 2I as well as in 3C and 1C.

(3) Fig. 4 - it might make more sense to normalize Brp and Cac intensity as a percentage of baseline (PhTx at Is or Ib) rather than normalizing everything to control Ib. 

We have revised the graphs as suggested in Figure 4 and throughout.

(4) Page 5 bottom - REFS missing after Fig. 1E. 

Thank you for catching this. We have fixed it.

Reviewer #2 (Recommendations For The Authors): 

This reader found differentiating between low Pr sites (deep purple) and cac measurements (black) difficult in Fig 1B. You may consider depicting this differently. 

Thank you for this feedback. We have changed the color scheme to improve readability.

I found it difficult to discern the difference between experiments Fig 1E and Fig 1J. Why are individual dots distributed differently? 

The individual data points are the same as in 1E and 1F, but we have removed the individual NMJ dimensionality to combine all Is and Ib data points together along with best fit lines for comparison of their slopes. We have added text to the revised manuscript to clarify this.

Results section, second paragraph, add references, remove 'REF': We next investigated the correlation between Pr and VGCC levels and found that at type Is inputs, single-AZ Cac intensity positively correlates with Pr (Fig. 1E; REFS). 

Thank you. We have corrected this error.

eLife assessment

Calcium channels are key regulators of synaptic strength and plasticity. The authors generate new endogenous tags of the Drosophila channel Cac as well as auxiliary subunits to investigate distinct calcium channel functions at the fly NMJ, Is and Ib. They demonstrate functions for voltage-gated calcium channel subunits in promoting synaptic strength, diversity, and plasticity with a series of convincing analyses. The work is important and has broad implications. In addition, the newly developed tools should be quite beneficial for fly biologists.

Reviewer #1 (Public Review):

Calcium channels are key regulators of synaptic strength and plasticity, yet how these channels are differentially utilized to enable synaptic diversity is not clear. In this manuscript, the authors use new endogenous tagging of the Drosophila CaV2 channel Cac and three auxiliary subunits to investigate distinct calcium channel functions at two motor neuron subtypes at the fly NMJ, Is and Ib. Although it is clear from previous studies that Pr is higher at Is over Ib, it is not clear why. The authors confirm these differences using postsynaptic calcium imaging combined with post-hoc Cac-TdTomato imaging. Then, through a series of confocal and super resolution imaging studies, the authors describe differences in calcium channel and active zone structure between Is and Ib motor neuron terminals, and the role of Brp and homeostatic plasticity in regulating channel abundance. Finally, the authors show that while the CaBeta subunit is present at similar levels at Is and Ib active zones, there is an interesting reduction in Stj at Is active zones. The authors conclude that these differences in active zone structure and architecture contribute to the generation of the observed heterogeneity in synaptic strength.

Overall the manuscript is well written, and the successful generation of the new endogenous Cac tags (Td-Tomato, Halo) and CaBeta, stj, and stolid genes with V5 tags will be powerful reagents for the field to enable new studies on calcium channels in synaptic structure, function, and plasticity. There are also some interesting, though not entirely unexpected, findings regarding how Brp and homeostatic plasticity modulate calcium channel abundance. The key factors generating diversity in synaptic strength beyond simple Ca2+ influx are well articulated in framing this study. Beyond the particularly useful new reagents for the field presented, the new data demonstrating a concerted and coupled increase in Cac, Stj, and CaB together after plasticity provides an interesting new dimension to the study and a foundation for new work moving forward.

Comments on revision:

This is a much improved revised manuscript, where the authors have done an excellent job of responding to my initial concerns. In particular, the key factors generating diversity in synaptic strength beyond simple Ca2+ influx are better articulated in framing this study. Beyond the particularly useful new reagents for the field presented, the new data demonstrating a concerted and coupled increase in Cac, Stj, and CaB together after plasticity provides an interesting new dimension to the study and a foundation for new work moving forward.

Upon reflection, I think my initial review came across as a bit harsh, and I am happy to now update my original evaluation to better reflect the importance and impact of this very nice study. I commend the authors on an outstanding study.

Reviewer #2 (Public Review):

The authors aim to investigate how voltage-gated calcium channel number, organization, and subunit composition lead to changes in synaptic activity at tonic and phasic motor neuron terminals, or type Is and Ib motor neurons in Drosophila. These neuron subtypes generate widely different physiological outputs, and many investigations have sought to understand the molecular underpinnings responsible for these differences. Additionally, these authors explore not only static differences that exist during the third-instar larval stage of development but also use a pharmacological approach to induce homeostatic plasticity to explore how these neuronal subtypes dynamically change the structural composition and organization of key synaptic proteins contributing to physiological plasticity. The Drosophila neuromuscular junction (NMJ) is glutamatergic, the main excitatory neurotransmitter in the human brain, so these findings not only expand our understanding of the molecular and physiological mechanisms responsible for differences in motor neuron subtype activity, but also contribute to our understanding of how the human brain and nervous system functions.

The authors employ state-of-the-art tools and techniques such as single-molecule localization microscopy 3D STORM and create several novel transgenic animals using CRISPR to expand the molecular tools available for exploration of synaptic biology that will be of wide interest to the field. Additionally, the authors use a robust set of experimental approaches from active zone level resolution functional imaging from live preparations to electrophysiology and immunohistochemical analyses to explore and test their hypotheses. All data appear to be robustly acquired and analyzed using appropriate methodology. The authors make important advancements to our understanding of how the different motor neuron subtypes, phasic and tonic-like, exhibit widely varying electrical output despite the neuromuscular junctions having similar ultrastructural composition in the proteins of interest, voltage gated calcium channel cacophony (cac) and the scaffold protein Bruchpilot (brp). The authors reveal the ratio of brp:cac appears to be a critical determinant of release probability (Pr), and in particular, the packing density of VGCCs and availability of brp. Importantly, the authors demonstrate a brp-dependent increase in VGCC density following acute philanthotoxin perfusion (glutamate receptor inhibitor). This VGCC increase appears to be largely responsible for the presynaptic homeostatic plasticity (PHP) observable at the Drosophila NMJ. Lastly, the authors created several novel CRISPR-tagged transgenic lines to visualize the spatial localization of VGCC subunits in Drosophila. Two of these lines, CaV5-C and stjV5-N, express in motor neurons and in the nervous system, localize at the NMJ, and most strikingly, strongly correlate with Pr at tonic and phasic-like terminals.

eLife assessment

Feeding, the circadian rhythm, and the gut microbiota are all intimately linked, motivating new approaches to identify causal relationships while minimizing confounding factors. The authors employ an innovative combination of the stool softener lactulose and a defined 3-member gut microbiota to acutely induce gut bacterial metabolism in mice during the daytime, resulting in changes in the ileal expression of clock genes and altered feeding behavior. Together, this study utilizes solid methods to provide important new insights into the role of gut microbiota in the circadian rhythm, setting the stage for follow-on studies aimed at better understanding the mechanisms responsible.

Reviewer #1 (Public Review):

Greter et al. provide an interesting and creative use of lactulose as a "microbial metabolism" inducer, combined with tracking of H2 and other fermentation end products. The topic is timely and will likely be of broad interest to researchers studying nutrition, circadian rhythm, and gut microbiota. However, a couple of moderate to major concerns were noted that may impact the interpretation of the current data:

(1) Much of the data relies on housing gnotobiotic mice in metabolic cages, but I couldn't find any details of methods to assess contamination during multiple days of housing outside of gnotobiotic isolators/cages. Given the complexity of the metabolic cage system used, sterility would likely be incredibly challenging to achieve. More details needed to be included about how potential contamination of the mice was assessed, ideally with 16S rRNA gene sequencing data of the endpoint samples and/or qPCR for total colonization levels relative to the more targeted data shown.

(2) The language could be softened to provide a more nuanced discussion of the results. While lactulose does seem to induce microbial metabolism it also could have direct effects on the host due to its osmotic activity or other off-target effects. Thus, it seems more precise to just refer to lactulose specifically in the figure titles and relevant text. Additionally, the degree to which lactulose "disrupts the diurnal rhythm" isn't clear from the data shown, especially given that the markers of circadian rhythm rapidly recover from the perturbation. It is probably more precise to instead state that lactulose transiently induces fermentation during the light phase or something to that effect. The discussion could also be expanded to address what methods are available or could be developed to build upon the concepts here; for example, the use of genetic inducers of metabolism which may avoid the more complex responses to lactulose.

Despite these concerns, this was still an intriguing and valuable addition to the growing literature on the interface of the microbiome and circadian fields.

Reviewer #2 (Public Review):

Summary:

The authors aimed to investigate how microbial metabolites, such as hydrogen and short-chain fatty acids (SCFAs), influence feeding behavior and circadian gene expression in mice. Specifically, they sought to understand these effects in different microbial environments, including a reduced community model (EAM), germ-free mice, and SPF mice. The study was designed to explore the broader relationship between the gut microbiome and host circadian rhythms, an area that is not well understood. Through their experiments, the authors hoped to elucidate how microbial metabolism could impact circadian clock genes and feeding patterns, potentially revealing new mechanisms of gut microbiome-host interactions.

Strengths:

The manuscript presents a well-executed investigation into the complex relationship between microbial metabolites and circadian rhythms, with a particular focus on feeding behavior and gene expression in different mouse models. One of the major strengths of the work lies in its innovative use of a reduced community model (EAM) to isolate and examine the effects of specific microbial metabolites, which provides valuable insights into how these metabolites might influence host behavior and circadian regulation. The study also contributes to the broader understanding of the gut microbiome's role in circadian biology, an area that remains poorly understood. The experiments are thoughtfully designed, with a clear rationale that ties together the gut microbiome, metabolic products, and host physiological responses. The authors successfully highlight an intriguing paradox: the significant influence of microbial metabolites in the EAM model versus the lack of effect in germ-free and SPF mice, which adds depth to the ongoing exploration of microbial-host interactions. Despite some methodological concerns, the manuscript offers compelling data and opens up new avenues for research in the field of microbiome and circadian biology.

Weaknesses:

The manuscript, while providing valuable insights, has several methodological weaknesses that impact the overall strength of the findings. First, the process for stool collection lacks clarity, raising concerns about potential biases, such as the risk of coprophagia, which could affect the dry-to-wet weight ratio analysis and compromise the validity of these measurements. Additionally, the use of the term "circadian" in some contexts appears inaccurate, as "diurnal" might be more appropriate, especially given the uncertainty regarding whether the observed microbiome fluctuations are truly circadian. Another significant issue is the unexpected absence of an osmotic effect of lactulose in EAM mice, which contradicts the known properties of lactulose as an osmotic laxative. This finding requires further verification, including the use of a positive control, to ensure it is not artifactual. The presentation of qRT-PCR data as log2-fold changes, with a mean denominator, could introduce bias by artificially reducing variability, potentially leading to spurious findings or increased risk of Type I error. This approach may explain the unexpected activation of both the positive and negative limbs of the circadian clock. Moreover, the lack of detailed information on the primers and housekeeping genes used in the experiments is concerning, particularly given the importance of using non-circadian housekeeping genes for accurate normalization. The methods for measuring metabolic hormones, such as GLP-1 and GIP, are also not adequately described. If DPP-IV/protease inhibitor tubes were not used, the data could be unreliable due to the rapid degradation of these hormones by circulating proteases. Finally, the manuscript does not address the collection of hormone levels during both fasting and fed phases, a critical aspect for interpreting the metabolic impact of microbial metabolites. These methodological concerns collectively weaken the robustness of the study's results and warrant careful reconsideration and clarification by the authors.

Because of these weaknesses, the authors have partially achieved their aims by providing novel insights into the relationship between microbial metabolites and host circadian rhythms. The data do suggest that microbial metabolites can significantly influence feeding behavior and circadian gene expression in specific contexts. However, the unexpected absence of an osmotic effect of lactulose, the potential biases introduced by the log2-fold change normalization in qRT-PCR data, and the lack of clarity in critical methodological details weaken the overall conclusions. While the study provides valuable contributions to understanding the gut microbiome's role in circadian biology, the methodological weaknesses prevent a full endorsement of the authors' conclusions. Addressing these issues would be necessary to strengthen the support for their findings and fully achieve the study's aims.

Despite the methodological concerns raised, this work has the potential to make a significant impact on the field of circadian biology and microbiome research. The study's exploration of the interaction between microbial metabolites and host circadian rhythms in different microbial environments opens new avenues for understanding the complex interplay between the gut microbiome and host physiology. This research contributes to the growing body of evidence that microbial metabolites play a crucial role in regulating host behaviors and physiological processes, including feeding and circadian gene expression.

Reviewer #3 (Public Review):

Summary:

In the manuscript by Greter, et al., entitled "Acute targeted induction of gut-microbial metabolism affects host clock genes and nocturnal feeding" the authors are attempting to demonstrate that an acute exposure to a non-nutritive disaccharide (lactulose) promotes microbial metabolism that feeds back onto the host to impact circadian networks. The premise of the study is interesting and the authors have performed several thoughtful experiments to dissect these relationships, providing valuable insights for the field. However, the work presented does not necessarily support some of the conclusions that are drawn. For instance, lactulose is administered during the fasting period to mimic the impact of a feeding bout on the gut microbiota, but it would be important to perform this treatment during the fed state as well to show that the effects on food intake, etc. do not occur. To truly draw the conclusion that the current outcomes are directly connected to and mediated via an impact on the host circadian clock, it would be ideal to perform these studies in a circadian gene knock-out animal (i.e., Cry1 or Cry2 KO mice, or perhaps Bmal-VilCre tissue-specific KO mice). If the effects are lost in these animals, this would more concretely connect the current findings to the circadian clock gene network. Despite these reservations, the work is promising.

Strengths:

Attempting to disentangle nutrient acquisition from microbial fermentation and its impact on diurnal dynamics of gut microbes on host circadian rhythms is an important step for providing insights into these host-microbe interactions.

The authors utilize a novel approach in leveraging lactulose coupled with germ-free animals and metabolic cages fitted with detectors that can measure microbial byproducts of fermentation, particularly hydrogen, in real-time.

The authors consider several interesting aspects of lactulose delivery, including how it shifts osmotic balance as well as provides calculations that attempt to explain the caloric contribution of fermentation to the animal in the context of reduced food intake. This provides interesting fundamental insights into the role of microbial outputs on host metabolism.

Weaknesses:

While the authors have done a large amount of work to examine the osmotic vs. metabolic influence of lactulose delivery, the authors have not accounted for the enlarged cecum and increased cecal surface area in germ-free mice. The authors could consider an additional control of cecectomy in germ-free mice.

The authors have examined GI hormones as one possible mechanism for how food intake is altered by microbial fermentation of lactulose. However, the authors measure PYY and GLP-1 only at a single time point, stating that there are no differences between groups. Given the goal of the studies is to tie these findings back into circadian rhythms, it would be important to show if the diurnal patterns of these GI hormones are altered.

Considerations of other factors, such as conjugated vs. deconjugated bile acids, microbial bile salt hydrolase activity, and bile acid resorption, might be an important consideration for how lactulose elicits more influence on ileal circadian clock genes relative to cecum and colon.

Measurements of GI transit time (both whole gut and regional) would be an important for consideration for how lactulose might be impacting the ileum vs. cecum vs. colon.

Author response:

Reviewer #1 (Public Review):

Greter et al. provide an interesting and creative use of lactulose as a "microbial metabolism" inducer, combined with tracking of H2 and other fermentation end products. The topic is timely and will likely be of broad interest to researchers studying nutrition, circadian rhythm, and gut microbiota. However, a couple of moderate to major concerns were noted that may impact the interpretation of the current data:

(1)  Much of the data relies on housing gnotobiotic mice in metabolic cages, but I couldn't find any details of methods to assess contamination during multiple days of housing outside of gnotobiotic isolators/cages. Given the complexity of the metabolic cage system used, sterility would likely be incredibly challenging to achieve. More details needed to be included about how potential contamination of the mice was assessed, ideally with 16S rRNA gene sequencing data of the endpoint samples and/or qPCR for total colonization levels relative to the more targeted data shown.

We thank the reviewer for pointing out that we have not made the experimental setup clear in the text. One of the unique features of our metabolic cage setup is that the mice do not need to be housed outside gnotobiotic isolators, but that the whole system is placed inside an isolator. We have developed and published this system recently (Hoces et al, PLOS Biol 2022), including extensive testing for sterility/gnotobiosis. We will improve clarity in a revised version.

Given that 16S sequencing of germ-free mice will typically produce false positive reads, we used Blautia pseudococcoides as an indicator strain for contaminations. This strain is present in our SPF mouse colony, forms spores that are highly resilient to decontamination measures, and has been the most likely contaminant in our gnotobiotic system. We have checked for presence of this strain in the cecum content of all our animals at the end of each experiment, and only included experiments which had a B. pseudococcoides signal below threshold level.

(2)  The language could be softened to provide a more nuanced discussion of the results. While lactulose does seem to induce microbial metabolism it also could have direct effects on the host due to its osmotic activity or other off-target effects. Thus, it seems more precise to just refer to lactulose specifically in the figure titles and relevant text. Additionally, the degree to which lactulose "disrupts the diurnal rhythm" isn't clear from the data shown, especially given that the markers of circadian rhythm rapidly recover from the perturbation. It is probably more precise to instead state that lactulose transiently induces fermentation during the light phase or something to that effect. The discussion could also be expanded to address what methods are available or could be developed to build upon the concepts here; for example, the use of genetic inducers of metabolism which may avoid the more complex responses to lactulose.

The point about language is well taken. We tried to make the argument that what we call disruption of the diurnal rhythm is acute, meaning that it is not disrupting the rhythm "chronically" (i.e., for longer), but that it recovers rapidly from this transient disruption. Given the confusion this wording is causing we are rephrasing this in a new version of the manuscript.

We also appreciate the mention of concepts from our study that can be built on in future studies, and we will add a paragraph on potential further research.

Despite these concerns, this was still an intriguing and valuable addition to the growing literature on the interface of the microbiome and circadian fields.

We thank the reviewer for all their encouraging and constructive remarks!

Reviewer #2 (Public Review):

Summary:

The authors aimed to investigate how microbial metabolites, such as hydrogen and short-chain fatty acids (SCFAs), influence feeding behavior and circadian gene expression in mice.

Specifically, they sought to understand these effects in different microbial environments, including a reduced community model (EAM), germ-free mice, and SPF mice. The study was designed to explore the broader relationship between the gut microbiome and host circadian rhythms, an area that is not well understood. Through their experiments, the authors hoped to elucidate how microbial metabolism could impact circadian clock genes and feeding patterns, potentially revealing new mechanisms of gut microbiome-host interactions.

Strengths:

The manuscript presents a well-executed investigation into the complex relationship between microbial metabolites and circadian rhythms, with a particular focus on feeding behavior and gene expression in different mouse models. One of the major strengths of the work lies in its innovative use of a reduced community model (EAM) to isolate and examine the effects of specific microbial metabolites, which provides valuable insights into how these metabolites might influence host behavior and circadian regulation. The study also contributes to the broader understanding of the gut microbiome's role in circadian biology, an area that remains poorly understood. The experiments are thoughtfully designed, with a clear rationale that ties together the gut microbiome, metabolic products, and host physiological responses. The authors successfully highlight an intriguing paradox: the significant influence of microbial metabolites in the EAM model versus the lack of effect in germ-free and SPF mice, which adds depth to the ongoing exploration of microbial-host interactions. Despite some methodological concerns, the manuscript offers compelling data and opens up new avenues for research in the field of microbiome and circadian biology.

We thank the reviewer for their encouraging remarks, specifically on the surprising findings that microbial metabolism seems to affect circadian clock gene expression and behavior differently in EAM and SPF mice.

Weaknesses:

The manuscript, while providing valuable insights, has several methodological weaknesses that impact the overall strength of the findings. First, the process for stool collection lacks clarity, raising concerns about potential biases, such as the risk of coprophagia, which could affect the dry-to-wet weight ratio analysis and compromise the validity of these measurements.

We thank the reviewer for pointing out that our description of the specific methods used for collecting feces were presented in a somewhat confusing manner. In short, dry and wet fecal weights were determined based on fecal pellets that were freshly produced and directly collected from restrained mice. To determine total fecal output over time, we collected all fecal pellets produced in a 5 hour window in a cage, determined their dry weight, and then used the water content determined for fresh feces to calculate wet weight. Using this method, we cannot account for potential differences in coprophagia between the groups. However, this is not likely to affect the dry-to-wet ratio of fecal output in our results.

Additionally, the use of the term "circadian" in some contexts appears inaccurate, as "diurnal" might be more appropriate, especially given the uncertainty regarding whether the observed microbiome fluctuations are truly circadian.

Similarly to our answer to reviewer 1 above, we appreciate this remark about imprecise language and have addressed this issue in the text. Indeed, we do not think the microbiota fluctuations are truly circadian, but likely a result of the entrainment through the host's food intake.

Another significant issue is the unexpected absence of an osmotic effect of lactulose in EAM mice, which contradicts the known properties of lactulose as an osmotic laxative. This finding requires further verification, including the use of a positive control, to ensure it is not artifactual.

This is a good point. We have used this lactulose dosage specifically to induce microbial metabolism without causing osmotic diarrhea, and went to some lengths do demonstrate this. In response to this comment (and one by reviewer 3 below about transit time), we are planning an experiment that will use a higher lactulose dose as a positive control.

The presentation of qRT-PCR data as log2-fold changes, with a mean denominator, could introduce bias by artificially reducing variability, potentially leading to spurious findings or increased risk of Type I error. This approach may explain the unexpected activation of both the positive and negative limbs of the circadian clock.

While we agree that our description of the qpcr method used for measuring circadian clock gene expression was lacking detail, we do not see how log2-fold changes (as opposed to, e.g., fold change) would lead to an increased risk of Type 1 error. We did not use a mean denominator for analyzing the data but used the house-keeping data for the same sample as denominator for the respective circadian clock genes. This will be described more clearly in a revised methods section.

Moreover, the lack of detailed information on the primers and housekeeping genes used in the experiments is concerning, particularly given the importance of using non-circadian housekeeping genes for accurate normalization.

We apologize for this omission, it seems like the resource table got lost in the submission, leading to missing information. It will be included in the revised manuscript.

The methods for measuring metabolic hormones, such as GLP-1 and GIP, are also not adequately described. If DPP-IV/protease inhibitor tubes were not used, the data could be unreliable due to the rapid degradation of these hormones by circulating proteases.

We thank the reviewer for spotting this mistake. We will add details of how GLP-1 and GIP were measured to the methods section. While we did not use DPP-IV/protease inhibitor tubes, we added the inhibitors to the syringes when sampling blood, leading to the same effect.

Finally, the manuscript does not address the collection of hormone levels during both fasting and fed phases, a critical aspect for interpreting the metabolic impact of microbial metabolites.

We agree that it will be interesting to measure hormone levels also in the fed phase, and we will include this data in a revised version of the manuscript. Even with that data, a more thorough examination of hormone levels over the diurnal cycle, as suggested by reviewer 3, might be relevant for a full-scale follow-up. Given our data, we of course cannot exclude that there may be time-point-specific differences and therefore have softened the language around this conclusion to state that hormone levels are not acutely changed after a lactulose intervention “at the time-points examined”.

These methodological concerns collectively weaken the robustness of the study's results and warrant careful reconsideration and clarification by the authors.

Because of these weaknesses, the authors have partially achieved their aims by providing novel insights into the relationship between microbial metabolites and host circadian rhythms. The data do suggest that microbial metabolites can significantly influence feeding behavior and circadian gene expression in specific contexts. However, the unexpected absence of an osmotic effect of lactulose, the potential biases introduced by the log2-fold change normalization in qRT- PCR data, and the lack of clarity in critical methodological details weaken the overall conclusions. While the study provides valuable contributions to understanding the gut microbiome's role in circadian biology, the methodological weaknesses prevent a full endorsement of the authors' conclusions. Addressing these issues would be necessary to strengthen the support for their findings and fully achieve the study's aims.

We thank the reviewer again for their careful and critical reading of our work, and for their constructive input. We hope that many of the concerns will be addressed by providing more methodological detail and additional experimental data in the revised version of our manuscript.

Despite the methodological concerns raised, this work has the potential to make a significant impact on the field of circadian biology and microbiome research. The study's exploration of the interaction between microbial metabolites and host circadian rhythms in different microbial environments opens new avenues for understanding the complex interplay between the gut microbiome and host physiology. This research contributes to the growing body of evidence that microbial metabolites play a crucial role in regulating host behaviors and physiological processes, including feeding and circadian gene expression.

We thank the reviewer for their encouraging remarks!

Reviewer #3 (Public Review):

Summary:

In the manuscript by Greter, et al., entitled "Acute targeted induction of gut-microbial metabolism affects host clock genes and nocturnal feeding" the authors are attempting to demonstrate that an acute exposure to a non-nutritive disaccharide (lactulose) promotes microbial metabolism that feeds back onto the host to impact circadian networks. The premise of the study is interesting and the authors have performed several thoughtful experiments to dissect these relationships, providing valuable insights for the field. However, the work presented does not necessarily support some of the conclusions that are drawn. For instance, lactulose is administered during the fasting period to mimic the impact of a feeding bout on the gut microbiota, but it would be important to perform this treatment during the fed state as well to show that the effects on food intake, etc. do not occur.

This is a good point, and we will include an experiment addressing this in a revised version of the manuscript.

To truly draw the conclusion that the current outcomes are directly connected to and mediated via an impact on the host circadian clock, it would be ideal to perform these studies in a circadian gene knock-out animal (i.e., Cry1 or Cry2 KO mice, or perhaps Bmal-VilCre tissue- specific KO mice). If the effects are lost in these animals, this would more concretely connect the current findings to the circadian clock gene network.

We agree that these would be interesting experiments to follow up on the question how the observed effects are actuated by host functions. However, they would require a large amount of preparatory work (including rederiving the KO mice to get them germ-free in our gnotobiotic facility), we argue that they are beyond the scope of this study.

Despite these reservations, the work is promising.

We thank the reviewer for their encouraging assessment.

Strengths:

Attempting to disentangle nutrient acquisition from microbial fermentation and its impact on diurnal dynamics of gut microbes on host circadian rhythms is an important step for providing insights into these host-microbe interactions.

The authors utilize a novel approach in leveraging lactulose coupled with germ-free animals and metabolic cages fitted with detectors that can measure microbial byproducts of fermentation, particularly hydrogen, in real-time.

The authors consider several interesting aspects of lactulose delivery, including how it shifts osmotic balance as well as provides calculations that attempt to explain the caloric contribution of fermentation to the animal in the context of reduced food intake. This provides interesting fundamental insights into the role of microbial outputs on host metabolism.

Thank you!

Weaknesses:

While the authors have done a large amount of work to examine the osmotic vs. metabolic influence of lactulose delivery, the authors have not accounted for the enlarged cecum and increased cecal surface area in germ-free mice. The authors could consider an additional control of cecectomy in germ-free mice.

We thank the reviewer for pointing out the potential effect of the anatomical differences of germ- free and conventionally colonized mice. We agree that when comparing germ-free mice to SPF mice, the enlarged cecum area in germ-free animals could lead to differences in water release or uptake. However, this is not the case in the gnotobiotic mice colonized with our minimal microbiota, which have comparable cecum sizes to germ-free mice, and thus comparing water transport over the cecum wall between those groups can be done without correcting for cecal surface areas. We will add information on cecum sizes in the different experimental groups to a revised version of the manuscript.

The authors have examined GI hormones as one possible mechanism for how food intake is altered by microbial fermentation of lactulose. However, the authors measure PYY and GLP-1 only at a single time point, stating that there are no differences between groups. Given the goal of the studies is to tie these findings back into circadian rhythms, it would be important to show if the diurnal patterns of these GI hormones are altered.

We fully agree that a deeper investigation of the diurnal fluctuations of hormone levels would be an interesting next step in studying whether perturbations in food intake can disturb these rhythms. Doing this for the whole rhythm would really require a full second study. For a revised version of this manuscript, we will add a second time-point of hormone measurements (during the fed phase) to this study. In addition, we will soften the statements made around these data to point out just that hormone level fluctuations could not be detected during specific time points after lactulose treatment, and therefore do not seem to explain the imminent behavioral changes.

Considerations of other factors, such as conjugated vs. deconjugated bile acids, microbial bile salt hydrolase activity, and bile acid resorption, might be an important consideration for how lactulose elicits more influence on ileal circadian clock genes relative to cecum and colon.

We absolutely agree that investigation of microbial bile acid modification and their metabolism by the host would be an interesting topic for a follow-up study.

Measurements of GI transit time (both whole gut and regional) would be an important for consideration for how lactulose might be impacting the ileum vs. cecum vs. colon.

This is also an interesting point, and we will add an assessment of transit time to a revised version of the manuscript.