Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

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

In this manuscript, the authors employed fast MAS NMR spectroscopy to investigate the gel aggregation of longer repeat (48×) RNAs, revealing inherent folding structures and interactions (i.e., G-quadruplex and duplex). The dynamic structure of the RNA gel was not resolved at high resolution, and only the structural features-namely, the coexistence of G-quadruplexes and duplexes-were inferred. The 1D and 2D NMR spectra were not assigned to specific atomic positions within the RNA, which makes it difficult to perform molecular dynamics (MD) modeling to elucidate the dynamic nature of the RNA gel. The following comments are provided for the authors' consideration:

Reviewer #1, Comment 1:

Figure 2E and Figure 3A: The data suggest that Ca²⁺ promotes stronger G-quadruplex formation within the RNA gel compared with Mg²⁺. This observation is somewhat puzzling, as Mg²⁺ is generally known to stabilize G-quadruplex structures. The authors should clarify this discrepancy.

__Response: __Mg2+ is also a stabilizer of double-stranded RNA. In most cases, Mg²⁺ stabilizes RNA duplexes more significantly than it stabilizes G-quadruplexes. When Mg2+ is removed and replaced for Ca2+, RNA duplex is destabilized more than G4 structures. We have added a clarification regarding that to the Conclusions section.

Reviewer #1, Comment 2:

Figures 2 and 3: The authors use the chemical shift at δN 144.1 ppm to distinguish between G-quadruplex and duplex structures. How was the reliability of this assignment evaluated? Chemical shifts of RNA atoms can be influenced by various factors such as intermolecular interactions, conformational stress, and local chemical environment, not only by higher-order structures. This point should be substantiated by citing relevant references or by analyzing additional RNA structures exhibiting δN 144.1 ppm signals using NMR spectroscopy.

Response: The assignment was made by comparing the chemical shifts with published data and by comparing the obtained spectra with existing datasets in the lab. We have added an explanation to the Results section and cited the literature. The 144.1 ppm was an illustrative value selected for guiding the discussion and we noted that it could sound too specific. We modified Figure 2 to outline the regions of chemical shifts in accordance with our interpretation of spectra.

Reviewer #1, Comment 3:

The authors state that "Our findings demonstrate that fast MAS NMR spectroscopy enables atomic-resolution monitoring of structural changes in GGGGCC repeat RNA of physiological lengths." This claim appears overstated, as no molecular model was constructed to define atomic coordinates based on NMR restraints.

Response: We agree and we have rewritten the conclusions to be more precise in wording. The new text does not mention “atomic-resolution” anymore.

Reviewer #1, Comment 4: Figure 3B: The experiment using nuclear extracts supplemented with Mg²⁺ to study RNA aggregation via 2D NMR may not accurately reflect intracellular conditions. It would be informative to perform a parallel experiment using nuclear extracts without additional Mg²⁺ to better simulate the native environment for RNA folding.

__Response: __We agree that we have not yet approached physiological conditions and that it would be interesting to obtain data for conditions at physiological Mg2+ concentrations in the range between 0.5 mM – 1 mM. The buffer of purchased nuclear extracts does not contain MgCl2, so some MgCl2 would still need to be added. In our opinion, nuclear extracts are actually not the optimal way to move forward, since they still differ from real in cell environment with the caveat that their composition is not well controlled. Full reconstitution with recombinant proteins might be a better approach because stoichiometry can be better regulated.

__Reviewer #1 (Significance (Required)): __ In this manuscript, the authors employed fast MAS NMR spectroscopy to investigate the gel aggregation of longer repeat (48×) RNAs, revealing inherent folding structures and interactions (i.e., G-quadruplex and duplex). The dynamic structure of the RNA gel was not resolved at high resolution, and only the structural features-namely, the coexistence of G-quadruplexes and duplexes-were inferred. The 1D and 2D NMR spectra were not assigned to specific atomic positions within the RNA, which makes it difficult to perform molecular dynamics (MD) modeling to elucidate the dynamic nature of the RNA gel.

Response: We agree that constraints for molecular dynamics cannot be derived from these data. The focus of this work is methodological: to demonstrate how 1H-15N 2D correlation spectra can be used to characterize G-G pairing in RNA gels directly. Such spectra could be used to study effects of small molecules or interacting proteins for example.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __ The manuscript by Kragelj et al. has the potential to become a valuable study demonstrating the role and power of modern solid-state NMR spectroscopy in investigating molecular assemblies that are otherwise inaccessible to other structural biology techniques. However, due to poor experimental execution and incomplete data interpretation, the manuscript requires substantial revision before it can be considered for publication in any journal.

__Reviewer #2, Major Concern __Inspection of the analytical gels of the transcribed RNA clearly shows that the desired RNA product constitutes only about 10% of the total crude transcript. The RNA must therefore be purified, for example by preparative PAGE, before performing any NMR or other biophysical studies. As it stands, all spectra shown in the figures represent a combined signal of all products in the crude mixture rather than the intended 48 repeat RNA. Consequently, all analyses and conclusions currently refer to a heterogeneous mixture of transcripts rather than the specific target RNA.

Response: The estimate of 10% 48xG4C2 on the gel is an overstatement. While multiple bands are visible, they correspond to dimers or multimers of the 48xG4C2 RNA. Transcripts that are longer than 48xG4C2 cannot occur in our transcription conditions. Bands at lower masses than expected are folded RNA. The high repeat length and the presence of Mg²⁺ during transcription promote multimerization, which is not fully reversed by denaturation in urea. If shorter transcripts had arisen from early termination they would be still substantially longer than 24 repeats based of what is visible on the gel and would thus remain within the pathological length range. Therefore, the observed NMR spectra primarily report on 48 repeat lengths.

__Reviewer #2, Specific Comments 1: __The statements: "We show that a technique called NMR spectroscopy under fast Magic Angle Spinning (fast MAS NMR) can be used to obtain structural information on GGGGCC repeat RNAs of physiological lengths. Fast MAS NMR can be used to obtain structural information on biomolecules regardless of their size." on page 1 are not entirely correct. Firstly, not only fast MAS NMR but MAS NMR in general can provide structural information on biomolecules regardless of their size. Fast MAS primarily allows for ¹H-detected experiments, improves spectral resolution, and reduces the required sample amount. Conventional ¹³C-detected solid-state MAS NMR can provide very similar structural information. A more thorough review of relevant literature could help address this issue.

Response: We have clarified the distinction between MAS NMR and Fast MAS NMR in the introduction.

__Reviewer #2, Specific Comments 2: __Secondly, MAS NMR has already been applied to systems of comparable complexity - for instance, the (CUG)₉₇ repeat studied by the Goerlach group as early as 2005. That work provided a comprehensive structural characterization of a similar molecular assembly. The authors are strongly encouraged to cite these studies (e.g., Riedel et al., J. Biomol. NMR, 2005; Riedel et al., Angew. Chem., 2006).

Response: We added a mention of that study in the introduction.

Reviewer #2, Experimental Description 1: The experimental details are poorly documented and need to be described in sufficient detail for reproducibility. Specifically: 1. What was the transcription scale? What was the yield (e.g., xx mg RNA per 1 mL transcription reaction)?

Response: Between 3.5 mg and 4.5 mg per 10 ml transcription reaction. We’ve added this information to the methods.

Reviewer #2, Experimental Description 2: 2. Why was the transcription product not purified? Dialysis only removes small molecules, while all macromolecular impurities above the cutoff remain. What was the dialysis cutoff used?

Response: RNA was purified using dialysis and phenol-chloroform precipitation. We have added the information about molecular weight cutoff for dialysis membranes to the methods.

Reviewer #2, Experimental Description 3: 3. How much RNA was used for each precipitation experiment? Were the amounts normalized? For example, if 10 mg of pellet were obtained, what fraction of that mass corresponded to RNA? Was this ratio consistent across all samples?

Response: In the test gel formations, we used 180.0 µg per condition. We used 108.0 µg of RNA for gelation test in the presence of nuclear extracts. We have not determined the water content in the gels. We added this information to methods and results section.

Reviewer #2, Experimental Description 4: 4. Why is there a smaller amount of precipitate when nuclear extract (NE) or CaCl₂ is added?

Response: The apparent difference in pellet size may reflect variations in water content rather than RNA quantity. While the Figure 1 might entice to directly compare pellet weights across different ion series tests, our primary goal was to determine the minimal divalent-ion concentrations required to reproducibly obtain gels. We have added a clarification in the Results section and in the Figure 1 caption regarding the comparability of conditions

Reviewer #2, Experimental Description 5: 5. The authors should describe NE addition in more detail: What is the composition of NE? What buffer was used (particularly Mg²⁺ and salt concentrations)? Was a control performed with NE buffer-type alone (without NE)?

Response: We have added the full description of NE buffer to the methods section. Its composition is: 40 mM Tris pH 8.0, 100 mM KCl, 0.2 mM EDTA, 0.5 mM PMSF, 0.5 mM DTT, 25 % glycerol. After mixing the nuclear extract with RNA, the target buffer was: 20 mM Tris pH 8.0, 90 mM KCl, 0.1 mM EDTA, 0.25 mM PMSF, 0.75 mM DTT, 12.5% glycerol, and 10 mM MgCl2.

We have not performed a control with NE buffer-type alone but we confirmed separately that glycerol does not affect gel formation.

Reviewer #2, Experimental Description 6: 6. How much pellet/RNA material was actually packed into each MAS rotor?

Response: Starting with a 5 mg pellet, we packed a rotor with a volume of 3 µl. We added this information to the methods section.

Reviewer #2, Additional Clarifications: P5. What is meant by "selective" in the phrase "We recorded a selective 1D-¹H MAS NMR spectrum of 48×G₄C₂ RNA gels"?

Response: That was a typo. We meant imino-selective. It is now corrected.

__Reviewer #2, Additional Clarifications: __ There are also several contradictions between statements in the text and the corresponding figures. For example: • Page 4: The authors write that "The addition of at least 5 mM Mg²⁺ was required for significant 48×G₄C₂ aggregation." However, Figure 1E shows significant aggregation already at 3 mM MgCl₂ (NE−), and in samples containing NE, aggregation appears even at 1 mM MgCl₂. Was aggregation already present in the sample containing NE but without any added MgCl₂?

Response: We changed text in the results section to more closely align with what’s depicted on the figure. There was some aggregation present in the nuclear extracts but it was of different quantity and quality. We clarified this in the results section.

__Reviewer #2 (Significance (Required)): __ The manuscript by Kragelj et al. has the potential to become a valuable study demonstrating the role and power of modern solid-state NMR spectroscopy in investigating molecular assemblies that are otherwise inaccessible to other structural biology techniques.

In its current form, tthe manuscript has significant experimental concerns - particularly the lack of RNA purification and inadequate description of materials and methods. The data therefore cannot support the conclusions presented. I recommend extensive revision and repetition of the experiments using purified RNA material before further consideration for publication.

__Response: __We’ve addressed the concerns about RNA purification within the response to the first comment (Major concern).

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __ This is an interesting manuscript reporting evidence for formation of both hairpins and G-quadruplexes within RNA aggregates formed by ALS expansion repeats (GGGGCC)n. This is in line with literature but never directly confirmed. Given the novelty of the method (NMR magic angle) and of the data (NMR on aggregate), I believe this manuscript should be considered for publication. I also trust the methods are appropriately reported and reproducible.

Below are my main points:

Major points:

__Reviewer #3, Comment 1: __ 1) RNA aggregation of the GGGGCCn repeat has been reported for expansion as short as 6-8 repeats (see Raguseo et al. Nat Commun 2023), so the authors might not see aggregation under the conditions they use for these shorter repeats but this can happen under physiological conditions . The ionic strengths and the conditions used can vary heavily the phase diagram and the authors therefore should tone down significantly their conclusions. They characterise one aggregate that is likely to contain both secondary structures under the conditions used (in terms of ion and pHs). However, it has been shown in Raguseo et al that aggregates can arise by both intermolecular G4s and hairpins (or a mixture of them) depending on the ionic conditions used. This means that what the authors report might not be necessarily relevant in cells, which should be caveated in the manuscript.

__Response: __We toned down our statements regarding aggregation of shorter repeats in the introduction. We added the citation to Raguseo et al. Nat Commun 2023, which indeed provides useful insights about aggregation of GGGGCC repeats. In Supplementary Figure 1, we had data on gel formation with 8x and 24x repeats which showed these repeat lengths form gels to some extent. We oversimplified our conclusion and said there were no aggregates which needs correction, especially considering other studies reported in the literature have observed in vitro aggregation of these repeat lengths. We modified the results section to reflect this nuance.

__Reviewer #3, Comment 2: __ 2) It would be important to perform perturbation experiments that might promote/disrupt formation of the G4 or hairpin and see if this affect RNA aggregation, which has been already reported by Raguseo et al, and wether this can be appreciated spectroscopically in their assay. This can be done by taking advantage of some of the experiments reported in the manuscript mentioned above, such as: PDS treatment (favouring monomolecular G4s and preventing aggregation), Li vs K treatment (favouring hairpin over G4s), NMM photo-oxidation (disassembling G4s) or addition of ALS relevant RNA binding proteins (i.e. TDP-43). Not all of these controls need to be performed but it would be good to reconcile how the fraction of G4 vs hairpin reflect aggregates' properties, since the authors offer such a nice technique to measure this.

Response: We appreciate the reviewer’s suggestions and we would be eager to do the perturbation experiments in the future. However, these experiments would require additional optimization and waiting for approval and availability of measurement time on a high-field NMR spectrometer. Given that the primary goal of this manuscript is reporting on the methodological approach, we think the current data adequately demonstrate the technique’s utility.

__Reviewer #3, Comment 3: __ 3) I disagree with the speculation of the monomolecular G4 being formed within the condensates, as the authors have no evidence to support this. It has been shown that n=8 repeat forms multimolecular G4s that are responsible of aggregation, so the authors need to provide direct evidence to support this hypothesis if they want to keep it in the manuscript, as it would clash with previous reports (Raguseo et al Nat Commun 2023)

Response: We agree that multimolecular G4s contribute to aggregation in our 48xG4C2 gels. We also realized, after reading this comment, that the original presentation of data and schematics may have unintentionally suggested the presence of monomolecular G4 in our RNA gels. To address this, we have added a clarification to the results section, we modified Figure 2 and 3, and we included a new Supplementary Figure 4. For clarification, both multimolecular and monomolecular G4s in model oligonucleotides produce imino 1H and 15N chemical shifts in the same region and cannot be distinguished by the experiments used in our study. Based on the observations reported in the literature, we believe that G4s in 48xG4C2 form primarily intermolecularly, although direct experimental proof is not available with the present data.

Minor points:

__Reviewer #3, Comment 4: __ 4) An obvious omission in the literature is Raguseo et al Nat Commun 2023, extensively mentioned above. Given the relevance of the findings reported in this manuscript for this study, this should be appropriately referenced for clarity.

Response: We’ve added the citation to Raguseo et al Nat Commun 2023 to the introduction where in vitro aggregation is discussed.

__Reviewer #3, Comment 5: __ 5) The schematic in Figure 3 is somehow confusing and the structures reported and how they relate to aggregate formation is not clear. Given that in structural studies presentation and appearance is everything, I would strongly recommend to the authors to improve the clarity of the schematic for the benefit of the readers.

Response: We thank you for your comment. We’ve modified the figure, and we hope it is now clearer.

Providing that the authors can address the criticisms raised, I would be supportive of publication of this fine study.

Reviewer #3 (Significance (Required)):

The main strength of this paper is to provide direct evidence of DNA secondary structure formation within aggregates, which is something that has not been done before. This is important as it reconcile with the relevance of hairpin formation for the disease (reported by Disney and co-workers) and the relevance of G4-formation in the process of aggregation through multimolecular G4-formation (reported by Di Antonio and co-workers). Given the significance of the findings in this context and the novelty of the method applied to the study of RNA aggregation, this reviewer is supportive for publication of this manuscript and of its relevance to the field. I would be, however, more careful in the conclusions reported and would add additional controls to strengthen the conclusions.

Response: We thank the reviewer for the comment. In the conclusion section, we have added a statement highlighting the potential roles of both double-stranded and G4 structures in gel formation, in line with what has been reported in previous studies.

Author response:

A major point all three reviewers raise is that the ‘human-AI collaboration’ in our experiment may not be true collaboration (as the AI does not classify images per se), but that it is only implied. The reviewers pointed out that whether participants were genuinely engaged in our experimental task is currently not sufficiently addressed. We plan to address this issue in the revised manuscript by including results from a brief interview we conducted after the experiment with each participant, which asked about the participant’s experience and decision-making processes while performing the task. Additionally, we also measured the participants’ propensity to trust in AI via a questionnaire before and after the experiment. The questionnaire and interview results will allow us to more accurately describe the involvement of our participants in the task. Additionally, we will conduct additional analyses of the behavioural data (e.g., response times) to show that participants genuinely completed the experimental task. Finally, we will work to sharpen our language and conclusions in the revised manuscript, following the reviewers’ recommendations.

Reviewer #1:

Summary:

In the study by Roeder and colleagues, the authors aim to identify the psychophysiological markers of trust during the evaluation of matching or mismatching AI decision-making. Specifically, they aim to characterize through brain activity how the decision made by an AI can be monitored throughout time in a two-step decision-making task. The objective of this study is to unfold, through continuous brain activity recording, the general information processing sequence while interacting with an artificial agent, and how internal as well as external information interact and modify this processing. Additionally, the authors provide a subset of factors affecting this information processing for both decisions.

Strengths:

The study addresses a wide and important topic of the value attributed to AI decisions and their impact on our own confidence in decision-making. It especially questions some of the factors modulating the dynamical adaptation of trust in AI decisions. Factors such as perceived reliability, type of image, mismatch, or participants' bias toward one response or the other are very relevant to the question in human-AI interactions.

Interestingly, the authors also question the processing of more ambiguous stimuli, with no real ground truth. This gets closer to everyday life situations where people have to make decisions in uncertain environments. Having a better understanding of how those decisions are made is very relevant in many domains.

Also, the method for processing behavioural and especially EEG data is overall very robust and is what is currently recommended for statistical analyses for group studies. Additionally, authors provide complete figures with all robustness evaluation information. The results and statistics are very detailed. This promotes confidence, but also replicability of results.

An additional interesting method aspect is that it is addressing a large window of analysis and the interaction between three timeframes (evidence accumulation pre-decision, decision-making, post-AI decision processing) within the same trials. This type of analysis is quite innovative in the sense that it is not yet a standard in complex experimental designs. It moves forward from classical short-time windows and baseline ERP analysis.

We appreciate the constructive appraisal of our work.

Weaknesses:

R1.1. This manuscript raises several conceptual and theoretical considerations that are not necessarily answered by the methods (especially the task) used. Even though the authors propose to assess trust dynamics and violations in cooperative human-AI teaming decision-making, I don't believe their task resolves such a question. Indeed, there is no direct link between the human decision and the AI decision. They do not cooperate per se, and the AI decision doesn't seem, from what I understood to have an impact on the participants' decision making. The authors make several assumptions regarding trust, feedback, response expectation, and "classification" (i.e., match vs. mismatch) which seem far stretched when considering the scientific literature on these topics.

This issue is raised by the other reviewers as well. The reviewer is correct in that the AI does not classify images but that the AI response is dependent on the participants’ choice (agree in 75% of trials, disagree in 25% of the trials). Importantly, though, participants were briefed before and during the experiment that the AI is doing its own independent image classification and that human input is needed to assess how well the AI image classification works. That is, participants were led to believe in a genuine, independent AI image classifier on this experiment.

Moreover, the images we presented in the experiment were taken from previous work by Nightingale & Farid (2022). This image dataset includes ‘fake’ (AI generated) images that are indistinguishable from real images.

What matters most for our work is that the participants were truly engaging in the experimental task; that is, they were genuinely judging face images, and they were genuinely evaluating the AI feedback. There is strong indication that this was indeed the case. We conducted and recorded brief interviews after the experiment, asking our participants about their experience and decision-making processes. The questions are as follows:

(1) How did you make the judgements about the images?

(2) How confident were you about your judgement?

(3) What did you feel when you saw the AI response?

(4) Did that change during the trials?

(5) Who do you think it was correct?

(6) Did you feel surprised at any of the AI responses?

(7) How did you judge what to put for the reliability sliders?

In our revised manuscript we will conduct additional analyses to provide detail on participants’ engagement in the task; both in the judging of the AI faces, as well as in considering the AI feedback. In addition, we will investigate the EEG signal and response time to check for effects that carry over between trials. We will also frame our findings more carefully taking scientific literature into account.

Nightingale SJ, and Farid H. "AI-synthesized faces are indistinguishable from real faces and more trustworthy." Proceedings of the National Academy of Sciences 119.8 (2022): e2120481119.

R1.2. Unlike what is done for the data processing, the authors have not managed to take the big picture of the theoretical implications of their results. A big part of this study's interpretation aims to have their results fit into the theoretical box of the neural markers of performance monitoring.

We indeed used primarily the theoretical box of performance monitoring and predictive coding, since the make-up of our task is similar to a more classical EEG oddball paradigm. In our revised manuscript, we will re-frame and address the link of our findings with the theoretical framework of evidence accumulation and decision confidence.

R1.3. Overall, the analysis method was very robust and well-managed, but the experimental task they have set up does not allow to support their claim. Here, they seem to be assessing the impact of a mismatch between two independent decisions.

Although the human and AI decisions are independent in the current experiment, the EEG results still shed light on the participant’s neural processes, as long as the participant considers the AI’s decision and believes it to be genuine. An experiment in which both decisions carry effective consequences for the task and the human-AI cooperation would be an interesting follow-up study.

Nevertheless, this type of work is very important to various communities. First, it addresses topical concerns associated with the introduction of AI in our daily life and decisions, but it also addresses methodological difficulties that the EEG community has been having to move slowly away from the static event-based short-timeframe analyses onto a more dynamic evaluation of the unfolding of cognitive processes and their interactions. The topic of trust toward AI in cooperative decision making has also been raised by many communities, and understanding the dynamics of trust, as well as the factors modulating it, is of concern to many high-risk environments, or even everyday life contexts. Policy makers are especially interested in this kind of research output.

Reviewer #2:

Summary:

The authors investigated how "AI-agent" feedback is perceived in an ambiguous classification task, and categorised the neural responses to this. They asked participants to classify real or fake faces, and presented an AI-agent's feedback afterwards, where the AI-feedback disagreed with the participants' response on a random 25% of trials (called mismatches). Pre-response ERP was sensitive to participants' classification as real or fake, while ERPs after the AI-feedback were sensitive to AI-mismatches, with stronger N2 and P3a&b components. There was an interaction of these effects, with mismatches after a "Fake" response affecting the N2 and those after "Real" responses affecting P3a&b. The ERPs were also sensitive to the participants' response biases, and their subjective ratings of the AI agent's reliability.

Strengths:

The researchers address an interesting question, and extend the AI-feedback paradigm to ambiguous tasks without veridical feedback, which is closer to many real-world tasks. The in-depth analysis of ERPs provides a detailed categorisation of several ERPs, as well as whole-brain responses, to AI-feedback, and how this interacts with internal beliefs, response biases, and trust in the AI-agent.

We thank the reviewer for their time in reading and reviewing our manuscript.

Weaknesses:

R2.1. There is little discussion of how the poor performance (close to 50% chance) may have affected performance on the task, such as by leading to entirely random guessing or overreliance on response biases. This can change how error-monitoring signals presented, as they are affected by participants' accuracy, as well as affecting how the AI feedback is perceived.

The images were chosen from a previous study (Nightingale & Farid, 2022, PNAS) that looked specifically at performance accuracy and also found levels around 50%. Hence, ‘fake’ and ‘real’ images are indistinguishable in this image dataset. Our findings agree with the original study.

Judging based on the brief interviews after the experiment (see answer to R.1.1.), all participants were actively and genuinely engaged in the task, hence, it is unlikely that they pressed buttons at random. As mentioned above, we will include a formal analysis of the interviews in the revised manuscript.

The response bias might indeed play a role in how participants responded, and this might be related to their initial propensity to trust in AI. We have questionnaire data available that might shed light on this issue: before and after the experiment, all participants answered the following questions with a 5-point Likert scale ranging from ‘Not True’ to ‘Completely True’:

(1) Generally, I trust AI.

(2) AI helps me solve many problems.

(3) I think it's a good idea to rely on AI for help.

(4) I don't trust the information I get from AI.

(5) AI is reliable.

(6) I rely on AI.

The propensity to trust questionnaire is adapted from Jessup SA, Schneider T R, Alarcon GM, Ryan TJ, & Capiola A. (2019). The measurement of the propensity to trust automation. International Conference on Human-Computer Interaction.

Our initial analyses did not find a strong link between the initial (before the experiment) responses to these questions, and how images were rated during the experiment. We will re-visit this analysis and add the results to the revised manuscript.

Regarding how error-monitoring (or the equivalent thereof in our experiment) is perceived, we will analyse interview questions 3 (“What did you feel when you saw the AI response”) and 6 (“Did you feel surprised at any of the AI responses”) and add results to the revised manuscript.

The task design and performance make it hard to assess how much it was truly measuring "trust" in an AI agent's feedback. The AI-feedback is yoked to the participants' performance, agreeing on 75% of trials and disagreeing on 25% (randomly), which is an important difference from the framing provided of human-AI partnerships, where AI-agents usually act independently from the humans and thus disagreements offer information about the human's own performance. In this task, disagreements are uninformative, and coupled with the at-chance performance on an ambiguous task, it is not clear how participants should be interpreting disagreements, and whether they treat it like receiving feedback about the accuracy of their choices, or whether they realise it is uninformative. Much greater discussion and justification are needed about the behaviour in the task, how participants did/should treat the feedback, and how these affect the trust/reliability ratings, as these are all central to the claims of the paper.

In our experiment, the AI disagreements are indeed uninformative for the purpose of making a correct judgment (that is, correctly classifying images as real or fake). However, given that the AI-generated faces are so realistic and indistinguishable from the real faces, the correctness of the judgement is not the main experimental factor in this study. We argue that, provided participants were genuinely engaged in the task, their judgment accuracy is less important than their internal experience when the goal is to examine processes occurring within the participants themselves. We briefed our participants as follows before the experiment:

“Technology can now create hyper-realistic images of people that do not exist. We are interested in your view on how well our AI system performs at identifying whether images of people’s faces are real or fake (computer-generated). Human input is needed to determine when a face looks real or fake. You will be asked to rate images as real or fake. The AI system will also independently rate the images. You will rate how reliable the AI is several times throughout the experiment.”

We plan to more fully expand the behavioural aspect and our participants’ experience in the revised manuscript by reporting the brief post-experiment interview (R.1.1.), the propensity to trust questionnaire (R.2.1.), and additional analyses of the response times.

There are a lot of EEG results presented here, including whole-brain and window-free analyses, so greater clarity on which results were a priori hypothesised should be given, along with details on how electrodes were selected for ERPs and follow-up tests.

We chose the electrodes mainly to be consistent across findings, and opted to use central electrodes (Pz and Fz), as long as the electrode was part of the electrodes within the reported cluster. We can in our revised manuscript also report on the electrodes with the maximal statistic, as part of a more complete and descriptive overview. We will also report on where we expected to see ERP components within the paper. In short, we did expect something like a P3, and we did also expect to see something before the response what we call the CPP. The rest of the work was more exploratory, with a more careful expectation that bias would be connected to the CPP, and the reliability ratings more to the P3; however, we find the opposite results. We will include this in our revised work as well.

We selected the electrodes primarily to maintain consistency across our findings and figures, and focused on central electrodes (Pz and Fz), provided they fell within the reported cluster. In the revised manuscript, we will also report the electrodes showing the maximal statistical effects to give a more complete and descriptive overview. Additionally, we will report where we expected specific ERP components to appear. In brief, we expected to see a P3 component post AI feedback, and a pre-response signal corresponding to the CPP. Beyond these expectations, the remaining analyses were more exploratory. Although we tentatively expected bias to relate to the CPP and reliability ratings to the P3, our results showed the opposite pattern. We will clarify this in the revised version of the manuscript.

Reviewer #3:

The current paper investigates neural correlates of trust development in human-AI interaction, looking at EEG signatures locked to the moment that AI advice is presented. The key finding is that both human-response-locked EEG signatures (the CPP) and post-AI-advice signatures (N2, P3) are modulated by trust ratings. The study is interesting, however, it does have some clear and sometimes problematic weaknesses:

(1) The authors did not include "AI-advice". Instead, a manikin turned green or blue, which was framed as AI advice. It is unclear whether participants viewed this as actual AI advice.

This point has been raised by the other reviewers as well, and we refer to the answers under R1.1., and under R2.1. We will address this concern by analysing the post-experiment interviews. In particular, questions 3 (“What did you feel when you saw the AI response”), 4 (“Did that change during the trials?”) and 6 (“Did you feel surprised at any of the AI responses”) will give critical insight. As stated above, our general impression from conducting the interviews is that all participants considered the robot icon as decision from an independent AI agent.

(2) The authors did not include a "non-AI" control condition in their experiment, such that we cannot know how specific all of these effects are to AI, or just generic uncertain feedback processing.

In the conceptualization phase of this study, we indeed considered different control conditions for our experiment to contrast different kinds of feedback. However, previous EEG studies on performance monitoring ERPs have reported similar results for human and machine supervision (Somon et al., 2019; de Visser et al., 2018). We therefore decided to focus on one aspect (the judgement of observation of an AI classification), also to prevent the experiment from taking too long and risking that participants would lose concentration and motivation to complete the experiment. Comparing AI vs non-AI feedback, is still interesting and would be a valuable follow-up study.

Somon B, et al. "Human or not human? Performance monitoring ERPs during human agent and machine supervision." NeuroImage 186 (2019): 266-277.

De Visser EJ, et al. "Learning from the slips of others: Neural correlates of trust in automated agents." Frontiers in human neuroscience 12 (2018): 309.

(3) Participants perform the task at chance level. This makes it unclear to what extent they even tried to perform the task or just randomly pressed buttons. These situations likely differ substantially from a real-life scenario where humans perform an actual task (which is not impossible) and receive actual AI advice.

This concern was also raised by the other two reviewers. As already stated in our responses above, we will add results from the post-experiment interviews with the participants, the propensity to trust questionnaire, and additional behavioural analyses in our revised manuscript.

Reviewer 1 (R1.3) also brought up the situation where decisions by the participant and the AI have a more direct link which carries consequences. This will be valuable follow-up research. In the revised manuscript, we will more carefully frame our approach.

(4) Many of the conclusions in the paper are overstated or very generic.

In the revised manuscript, we will re-phrase our discussion and conclusions to address the points raised in the reviewer’s recommendations to authors.

Racism in education, and introduces race into education.

This line makes sense to me because it explains how easy it is to stop questioning the media we see everyday. When something is constantly shown, like stereotypes in movies or the way certain groups are shown. It starts to feel normal even if it's totally inaccurate. This makes Hall's point, that we have to step back and actually think about what we're being shown instead of just absorbing it without realizing, clear.

Author response:

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

Reviewer #1 (Public review):

Summary:

From a forward genetic mosaic mutant screen using EMS, the authors identify mutations in glucosylceramide synthase (GlcT), a rate-limiting enzyme for glycosphingolipid (GSL) production, that result in EE tumors. Multiple genetic experiments strongly support the model that the mutant phenotype caused by GlcT loss is due to by failure of conversion of ceramide into glucosylceramide. Further genetic evidence suggests that Notch signaling is comprised in the ISC lineage and may affect the endocytosis of Delta. Loss of GlcT does not affect wing development or oogenesis, suggesting tissue-specific roles for GlcT. Finally, an increase in goblet cells in UGCG knockout mice, not previously reported, suggests a conserved role for GlcT in Notch signaling in intestinal cell lineage specification.

Strengths:

Overall, this is a well-written paper with multiple well-designed and executed genetic experiments that support a role for GlcT in Notch signaling in the fly and mammalian intestine. I do, however, have a few comments below.

Weaknesses:

(1) The authors bring up the intriguing idea that GlcT could be a way to link diet to cell fate choice. Unfortunately, there are no experiments to test this hypothesis.

We indeed attempted to establish an assay to investigate the impact of various diets (such as high-fat, high-sugar, or high-protein diets) on the fate choice of ISCs. Subsequently, we intended to examine the potential involvement of GlcT in this process. However, we observed that the number or percentage of EEs varies significantly among individuals, even among flies with identical phenotypes subjected to the same nutritional regimen. We suspect that the proliferative status of ISCs and the turnover rate of EEs may significantly influence the number of EEs present in the intestinal epithelium, complicating the interpretation of our results. Consequently, we are unable to conduct this experiment at this time. The hypothesis suggesting that GlcT may link diet to cell fate choice remains an avenue for future experimental exploration.

(2) Why do the authors think that UCCG knockout results in goblet cell excess and not in the other secretory cell types?

This is indeed an interesting point. In the mouse intestine, it is well-documented that the knockout of Notch receptors or Delta-like ligands results in a classic phenotype characterized by goblet cell hyperplasia, with little impact on the other secretory cell types. This finding aligns very well with our experimental results, as we noted that the numbers of Paneth cells and enteroendocrine cells appear to be largely normal in UGCG knockout mice. By contrast, increases in other secretory cell types are typically observed under conditions of pharmacological inhibition of the Notch pathway.

(3) The authors should cite other EMS mutagenesis screens done in the fly intestine.

To our knowledge, the EMS screen on 2L chromosome conducted in Allison Bardin’s lab is the only one prior to this work, which leads to two publications (Perdigoto et al., 2011; Gervais, et al., 2019). We have now included citations for both papers in the revised manuscript.

(4) The absence of a phenotype using NRE-Gal4 is not convincing. This is because the delay in its expression could be after the requirement for the affected gene in the process being studied. In other words, sufficient knockdown of GlcT by RNA would not be achieved until after the relevant signaling between the EB and the ISC occurred. Dl-Gal4 is problematic as an ISC driver because Dl is expressed in the EEP.

This is an excellent point, and we agree that the lack of an observable phenotype using NRE-Gal4 could be due to delayed expression, which may result in missing the critical window required for effective GlcT knockdown. Consequently, we cannot rule out the possibility that GlcT also plays a role in early EBs or EEPs. We have revised the manuscript to soften this conclusion and to include this alternative explanation for the experiment.

(5) The difference in Rab5 between control and GlcT-IR was not that significant. Furthermore, any changes could be secondary to increases in proliferation.

We agree that it is possible that the observed increase in proliferation could influence the number of Rab5+ endosomes, and we will temper our conclusions on this aspect accordingly. However, it is important to note that, although the difference in Rab5+ endosomes between the control and GlcT-IR conditions appeared mild, it was statistically significant and reproducible. In our revised experiments, we have not only added statistical data and immunofluorescence images for Rab11 but also unified the approaches used for detecting Rab-associated proteins (in the previous figures, Rab5 was shown using U-Rab5-GFP, whereas Rab7 was detected by direct antibody staining). Based on this unified strategy, we optimized the quantification of Dl-GFP colocalization with early, late, and recycling endosomes, and the results are consistent with our previous observations (see the updated Fig. 5).

Reviewer #2 (Public review):

Summary:

This study genetically identifies two key enzymes involved in the biosynthesis of glycosphingolipids, GlcT and Egh, which act as tumor suppressors in the adult fly gut. Detailed genetic analysis indicates that a deficiency in Mactosyl-ceramide (Mac-Cer) is causing tumor formation. Analysis of a Notch transcriptional reporter further indicates that the lack of Mac-Ser is associated with reduced Notch activity in the gut, but not in other tissues.

Addressing how a change in the lipid composition of the membranes might lead to defective Notch receptor activation, the authors studied the endocytic trafficking of Delta and claimed that internalized Delta appeared to accumulate faster into endosomes in the absence of Mac-Cer. Further analysis of Delta steady-state accumulation in fixed samples suggested a delay in the endosomal trafficking of Delta from Rab5+ to Rab7+ endosomes, which was interpreted to suggest that the inefficient, or delayed, recycling of Delta might cause a loss in Notch receptor activation.

Finally, the histological analysis of mouse guts following the conditional knock-out of the GlcT gene suggested that Mac-Cer might also be important for proper Notch signaling activity in that context.

Strengths:

The genetic analysis is of high quality. The finding that a Mac-Cer deficiency results in reduced Notch activity in the fly gut is important and fully convincing.

The mouse data, although preliminary, raised the possibility that the role of this specific lipid may be conserved across species.

Weaknesses:

This study is not, however, without caveats and several specific conclusions are not fully convincing.

First, the conclusion that GlcT is specifically required in Intestinal Stem Cells (ISCs) is not fully convincing for technical reasons: NRE-Gal4 may be less active in GlcT mutant cells, and the knock-down of GlcT using Dl-Gal4ts may not be restricted to ISCs given the perdurance of Gal4 and of its downstream RNAi.

As previously mentioned, we acknowledge that a role for GlcT in early EBs or EEPs cannot be completely ruled out. We have revised our manuscript to present a more cautious conclusion and explicitly described this possibility in the updated version.

Second, the results from the antibody uptake assays are not clear.: i) the levels of internalized Delta were not quantified in these experiments; ii) additionally, live guts were incubated with anti-Delta for 3hr. This long period of incubation indicated that the observed results may not necessarily reflect the dynamics of endocytosis of antibody-bound Delta, but might also inform about the distribution of intracellular Delta following the internalization of unbound anti-Delta. It would thus be interesting to examine the level of internalized Delta in experiments with shorter incubation time.

We thank the reviewer for these excellent questions. In our antibody uptake experiments, we noted that Dl reached its peak accumulation after a 3-hour incubation period. We recognize that quantifying internalized Dl would enhance our analysis, and we will include the corresponding statistical graphs in the revised version of the manuscript. In addition, we agree that during the 3-hour incubation, the potential internalization of unbound anti-Dl cannot be ruled out, as it may influence the observed distribution of intracellular Dl. We therefore attempted to supplement our findings with live imaging experiments to investigate the dynamics of Dl/Notch endocytosis in both normal and GlcT mutant ISCs. However, we found that the GFP expression level of Dl-GFP (either in the knock-in or transgenic line) was too low to be reliably tracked. During the three-hour observation period, the weak GFP signal remained largely unchanged regardless of the GlcT mutation status, and the signal resolution under the microscope was insufficient to clearly distinguish membrane-associated from intracellular Dl. Therefore, we were unable to obtain a dynamic view of Dl trafficking through live imaging. Nevertheless, our Dl antibody uptake and endosomal retention analyses collectively support the notion that MacCer influences Notch signaling by regulating Dl endocytosis.

Overall, the proposed working model needs to be solidified as important questions remain open, including: is the endo-lysosomal system, i.e. steady-state distribution of endo-lysosomal markers, affected by the Mac-Cer deficiency? Is the trafficking of Notch also affected by the Mac-Cer deficiency? is the rate of Delta endocytosis also affected by the Mac-Cer deficiency? are the levels of cell-surface Delta reduced upon the loss of Mac-Cer?

Regarding the impact on the endo-lysosomal system, this is indeed an important aspect to explore. While we did not conduct experiments specifically designed to evaluate the steady-state distribution of endo-lysosomal markers, our analyses utilizing Rab5-GFP overexpression and Rab7 staining did not indicate any significant differences in endosome distribution in MacCer deficient conditions. Moreover, we still observed high expression of the NRE-LacZ reporter specifically at the boundaries of clones in GlcT mutant cells (Fig. 4A), indicating that GlcT mutant EBs remain responsive to Dl produced by normal ISCs located right at the clone boundary. Therefore, we propose that MacCer deficiency may specifically affect Dl trafficking without impacting Notch trafficking.

In our 3-hour antibody uptake experiments, we observed a notable decrease in cell-surface Dl, which was accompanied by an increase in intracellular accumulation. These findings collectively suggest that Dl may be unstable on the cell surface, leading to its accumulation in early endosomes.

Third, while the mouse results are potentially interesting, they seem to be relatively preliminary, and future studies are needed to test whether the level of Notch receptor activation is reduced in this model.

In the mouse small intestine, Olfm4 is a well-established target gene of the Notch signaling pathway, and its staining provides a reliable indication of Notch pathway activation. While we attempted to evaluate Notch activation using additional markers, such as Hes1 and NICD, we encountered difficulties, as the corresponding antibody reagents did not perform well in our hands. Despite these challenges, we believe that our findings with Olfm4 provide an important start point for further investigation in the future.

Reviewer #3 (Public review):

Summary:

In this paper, Tang et al report the discovery of a Glycoslyceramide synthase gene, GlcT, which they found in a genetic screen for mutations that generate tumorous growth of stem cells in the gut of Drosophila. The screen was expertly done using a classic mutagenesis/mosaic method. Their initial characterization of the GlcT alleles, which generate endocrine tumors much like mutations in the Notch signaling pathway, is also very nice. Tang et al checked other enzymes in the glycosylceramide pathway and found that the loss of one gene just downstream of GlcT (Egh) gives similar phenotypes to GlcT, whereas three genes further downstream do not replicate the phenotype. Remarkably, dietary supplementation with a predicted GlcT/Egh product, Lactosyl-ceramide, was able to substantially rescue the GlcT mutant phenotype. Based on the phenotypic similarity of the GlcT and Notch phenotypes, the authors show that activated Notch is epistatic to GlcT mutations, suppressing the endocrine tumor phenotype and that GlcT mutant clones have reduced Notch signaling activity. Up to this point, the results are all clear, interesting, and significant. Tang et al then go on to investigate how GlcT mutations might affect Notch signaling, and present results suggesting that GlcT mutation might impair the normal endocytic trafficking of Delta, the Notch ligand. These results (Fig X-XX), unfortunately, are less than convincing; either more conclusive data should be brought to support the Delta trafficking model, or the authors should limit their conclusions regarding how GlcT loss impairs Notch signaling. Given the results shown, it's clear that GlcT affects EE cell differentiation, but whether this is via directly altering Dl/N signaling is not so clear, and other mechanisms could be involved. Overall the paper is an interesting, novel study, but it lacks somewhat in providing mechanistic insight. With conscientious revisions, this could be addressed. We list below specific points that Tang et al should consider as they revise their paper.

Strengths:

The genetic screen is excellent.

The basic characterization of GlcT phenotypes is excellent, as is the downstream pathway analysis.

Weaknesses:

(1) Lines 147-149, Figure 2E: here, the study would benefit from quantitations of the effects of loss of brn, B4GalNAcTA, and a4GT1, even though they appear negative.

We have incorporated the quantifications for the effects of the loss of brn, B4GalNAcTA, and a4GT1 in the updated Figure 2.

(2) In Figure 3, it would be useful to quantify the effects of LacCer on proliferation. The suppression result is very nice, but only effects on Pros+ cell numbers are shown.

We have now added quantifications of the number of EEs per clone to the updated Figure 3.

(3) In Figure 4A/B we see less NRE-LacZ in GlcT mutant clones. Are the data points in Figure 4B per cell or per clone? Please note. Also, there are clearly a few NRE-LacZ+ cells in the mutant clone. How does this happen if GlcT is required for Dl/N signaling?

In Figure 4B, the data points represent the fluorescence intensity per single cell within each clone. It is true that a few NRE-LacZ+ cells can still be observed within the mutant clone; however, this does not contradict our conclusion. As noted, high expression of the NRE-LacZ reporter was specifically observed around the clone boundaries in MacCer deficient cells (Fig. 4A), indicating that the mutant EBs can normally receive Dl signal from the normal ISCs located at the clone boundary and activate the Notch signaling pathway. Therefore, we believe that, although affecting Dl trafficking, MacCer deficiency does not significantly affect Notch trafficking.

(4) Lines 222-225, Figure 5AB: The authors use the NRE-Gal4ts driver to show that GlcT depletion in EBs has no effect. However, this driver is not activated until well into the process of EB commitment, and RNAi's take several days to work, and so the author's conclusion is "specifically required in ISCs" and not at all in EBs may be erroneous.

As previously mentioned, we acknowledge that a role for GlcT in early EBs or EEPs cannot be completely ruled out. We have revised our manuscript to present a more cautious conclusion and described this possibility in the updated version.

(5) Figure 5C-F: These results relating to Delta endocytosis are not convincing. The data in Fig 5C are not clear and not quantitated, and the data in Figure 5F are so widely scattered that it seems these co-localizations are difficult to measure. The authors should either remove these data, improve them, or soften the conclusions taken from them. Moreover, it is unclear how the experiments tracing Delta internalization (Fig 5C) could actually work. This is because for this method to work, the anti-Dl antibody would have to pass through the visceral muscle before binding Dl on the ISC cell surface. To my knowledge, antibody transcytosis is not a common phenomenon.

We thank the reviewer for these insightful comments and suggestions. In our in vivo experiments, we observed increased co-localization of Rab5 and Dl in GlcT mutant ISCs, indicating that Dl trafficking is delayed at the transition to Rab7⁺ late endosomes, a finding that is further supported by our antibody uptake experiments. We acknowledge that the data presented in Fig. 5C are not fully quantified and that the co-localization data in Fig. 5F may appear somewhat scattered; therefore, we have included additional quantification and enhanced the data presentation in the revised manuscript.

Regarding the concern about antibody internalization, we appreciate this point. We currently do not know if the antibody reaches the cell surface of ISCs by passing through the visceral muscle or via other routes. Given that the experiment was conducted with fragmented gut, it is possible that the antibody may penetrate into the tissue through mechanisms independent of transcytosis.

As mentioned earlier, we attempted to supplement our findings with live imaging experiments to investigate the dynamics of Dl/Notch endocytosis in both normal and GlcT mutant ISCs. However, we found that the GFP expression level of Dl-GFP (either in the knock-in or transgenic line) was too low to be reliably tracked. During the three-hour observation period, the weak GFP signal remained largely unchanged regardless of the GlcT mutation status, and the signal resolution under the microscope was insufficient to clearly distinguish membrane-associated from intracellular Dl. Therefore, we were unable to obtain a dynamic view of Dl trafficking through live imaging. Nevertheless, our Dl antibody uptake and endosomal retention analyses collectively support the notion that MacCer influences Notch signaling by regulating Dl endocytosis.

(6) It is unclear whether MacCer regulates Dl-Notch signaling by modifying Dl directly or by influencing the general endocytic recycling pathway. The authors say they observe increased Dl accumulation in Rab5+ early endosomes but not in Rab7+ late endosomes upon GlcT depletion, suggesting that the recycling endosome pathway, which retrieves Dl back to the cell surface, may be impaired by GlcT loss. To test this, the authors could examine whether recycling endosomes (marked by Rab4 and Rab11) are disrupted in GlcT mutants. Rab11 has been shown to be essential for recycling endosome function in fly ISCs.

We agree that assessing the state of recycling endosomes, especially by using markers such as Rab11, would be valuable in determining whether MacCer regulates Dl-Notch signaling by directly modifying Dl or by influencing the broader endocytic recycling pathway. In the newly added experiments, we found that in GlcT-IR flies, Dl still exhibits partial colocalization with Rab11, and the overall expression pattern of Rab11 is not affected by GlcT knockdown (Fig. 5E-F). These observations suggest that MacCer specifically regulates Dl trafficking rather than broadly affecting the recycling pathway.

(7) It remains unclear whether Dl undergoes post-translational modification by MacCer in the fly gut. At a minimum, the authors should provide biochemical evidence (e.g., Western blot) to determine whether GlcT depletion alters the protein size of Dl.

While we propose that MacCer may function as a component of lipid rafts, facilitating Dl membrane anchorage and endocytosis, we also acknowledge the possibility that MacCer could serve as a substrate for protein modifications of Dl necessary for its proper function. Conducting biochemical analyses to investigate potential post-translational modifications of Dl by MacCer would indeed provide valuable insights. We have performed Western blot analysis to test whether GlcT depletion affects the protein size of Dl. As shown below, we did not detect any apparent changes in the molecular weight of the Dl protein. Therefore, it is unlikely that MacCer regulates post-translational modifications of Dl.

Author response image 1.

To investigate whether MacCer modifies Dl by Western blot,(A) Four lanes were loaded: the first two contained 20 μL of membrane extract (lane 1: GlcT-IR, lane 2: control), while the last two contained 10 μL of membrane extract (B) Full blot images are shown under both long and shortexposure conditions.

(8) It is unfortunate that GlcT doesn't affect Notch signaling in other organs on the fly. This brings into question the Delta trafficking model and the authors should note this. Also, the clonal marker in Figure 6C is not clear.

In the revised working model, we have explicitly described that the events occur in intestinal stem cells. Regarding Figure 6C, we have delineated the clone with a white dashed line to enhance its clarity and visual comprehension.

(9) The authors state that loss of UGCG in the mouse small intestine results in a reduced ISC count. However, in Supplementary Figure C3, Ki67, a marker of ISC proliferation, is significantly increased in UGCG-CKO mice. This contradiction should be clarified. The authors might repeat this experiment using an alternative ISC marker, such as Lgr5.

Previous studies have indicated that dysregulation of the Notch signaling pathway can result in a reduction in the number of ISCs. While we did not perform a direct quantification of ISC numbers in our experiments, our Olfm4 staining—which serves as a reliable marker for ISCs—demonstrates a clear reduction in the number of positive cells in UGCG-CKO mice.

The increased Ki67 signal we observed reflects enhanced proliferation in the transit-amplifying region, and it does not directly indicate an increase in ISC number. Therefore, in UGCG-CKO mice, we observe a decrease in the number of ISCs, while there is an increase in transit-amplifying (TA) cells (progenitor cells). This increase in TA cells is probably a secondary consequence of the loss of barrier function associated with the UGCG knockout.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #3 (Recommendations for the authors):

The authors have done an excellent job of addressing most comments, but my concerns about Figure 5 remain. I appreciate the authors' efforts to address the problem involving Rs being part of the computation on both the x and y axes of Figure 5, but addressing this via simulation addresses statistical significance but overlooks effect size. I think the authors may have misunderstood my original suggestion, so I will attempt to explain it better here. Since "Rs" is an average across all trials, the trials could be subdivided in two halves to compute two separate averages - for example, an average of the even numbered trials and an average of the odd numbered trials. Then you would use the "Rs" from the even numbered trials for one axis and the "Rs" from the odd numbered trials for the other. You would then plot R-Rs_even vs Rf-Rs_odd. This would remove the confound from this figure, and allow the text/interpretation to be largely unchanged (assuming the results continue to look as they do).

We have added a description and the result of the new analysis (line #321 to #332), and a supplementary figure (Suppl. Fig. 1) (line #1464 to #1477). 

“We calculated 𝑅_𝑠 in the ordinate and abscissa of Figure 5A-E using responses averaged across different subsets of trials, such that 𝑅_𝑠 was no longer a common term in the ordinate and abscissa. For each neuron, we determined 𝑅_𝑠1 by averaging the firing rates of 𝑅_𝑠 across half of the recorded trials, selected randomly. We also determined 𝑅_𝑠2 by averaging the firing rates of 𝑅_𝑠 across the rest of the trials.  We regressed (𝑅 − 𝑅_𝑠1 )  on (𝑅_𝑓 − 𝑅_𝑠2) , as well as (𝑅_𝑠 - 𝑅_𝑠2)  on (𝑅_𝑓 − 𝑅_𝑠1), and repeated the procedure 50 times. The averaged slopes obtained with 𝑅_𝑠 from the split trials showed the same pattern as those using 𝑅_𝑠 from all trials (Table 1 and Supplementary Fig. 1), although the coefficient of determination was slightly reduced (Table 1). For ×4 speed separation, the slopes were nearly identical to those shown in Figure 5F1. For ×2 speed separation, the slopes were slightly smaller than those in Figure 5F2, but followed the same pattern (Supplementary Fig. 1). Together, these analysis results confirmed the faster-speed bias at the slow stimulus speeds, and the change of the response weights as stimulus speeds increased.”

An additional remaining item concerns the terminology weighted sum, in the context of the constraint that wf and ws must sum to one. My opinion is that it is non-standard to use weighted sum when the computation is a weighted average, but as long as the authors make their meaning clear, the reader will be able to follow. I suggest adding some phrasing to explain to the reader the shift in interpretation from the more general weighted sum to the more constrained weighted average. Specifically, "weighted sum" first appears on line 268, and then the additional constraint of ws + wf =1 is introduced on line 278. Somewhere around line 278, it would be useful to include a sentence stating that this constraint means the weighted sum is constrained to be a weighted average.

Thanks for the suggestion. We have modified the text as follows. Since we made other modifications in the text, the line numbers are slightly different from the last version. 

Line #274 to 275: 

“Since it is not possible to solve for both variables, 𝑤_𝑠 and 𝑤_𝑓, from a single equation (Eq. 5) with three data points, we introduced an additional constraint: 𝑤_𝑠 + 𝑤_𝑓 =1. With this constraint, the weighted sum becomes a weighted average.”

Also on line #309:

“First, at each speed pair and for each of the 100 neurons in the data sample shown in Figure 5, we simulated the response to the bi-speed stimuli (𝑅_𝑒) as a randomly weighted average of 𝑅_𝑓 and 𝑅_𝑠 of the same neuron. 

in which 𝑎 was a randomly generated weight (between 0 and 1) for 𝑅_𝑓, and the weights for 𝑅_𝑓 and 𝑅_𝑠 summed to one.”

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)): The authors map the ZFP36L1 protein interactome in human T cells using UltraID proximity labeling combined with quantitative mass spectrometry. They optimize labeling conditions in primary T cells, profile resting and activated cells, and include a time course at 2, 5, and 16 hours. They complement the interactome with co-immunoprecipitation in the presence or absence of RNase to assess RNA dependence. They then test selected candidates using CRISPR knockouts in primary T cells, focusing on UPF1 and GIGYF1/2, and report effects on global translation, stress, activation markers, and ZFP36L1 protein levels. The work argues that ZFP36L1 sits at the center of multiple post-transcriptional pathways in T cells (which in itself is not a novel finding) and that UPF1 supports ZFP36L1 expression at the mRNA and protein level. The main model system is primary human T cells, with some data in Jurkat cells.

The core datasets show thousands of identified proteins in total lysates and enriched biotinylated fractions. Known partners from CCR4-NOT, decapping, stress granules, and P-bodies appear, with additional candidates like GIGYF1/2, PATL1, DDX6, and UPF1. Time-resolved labeling suggests shifts in proximity during early activation. Co-IP with and without RNase suggests both RNA-dependent and RNA-independent contacts. CRISPR loss of UPF1 or GIGYF1/2 increases translation at rest and elevates activation markers, and UPF1 loss reduces ZFP36L1 protein and mRNA while MG132 does not rescue protein levels; UPF1 RIP enriches ZFP36L1 mRNA.

Among patterns worth noting are that the activation state drives the principal variance in both proteome and proximity datasets. Deadenylation, decapping, and granule proteins are consistently near ZFP36L1 across conditions, while some contacts dip at 2 hours and recover by 5 to 16 hours. Mitochondrial ribosomal proteins become more proximal later. UPF1 and GIGYF1 show time-linked behavior and RNase sensitivity that fits roles in mRNA surveillance and translational control. These observations support a dynamic hub model, though they remain proximity-based rather than direct binding maps.

We thank the reviewer for their careful reading and thoughtful summary. Please find our point-to point response below.

Major comments

1) The key conclusions are directionally convincing for a broad and dynamic ZFP36L1 neighborhood in human T cells. The data robustly recover established complexes and add plausible candidates. The time-course and RNase experiments strengthen the claim that interactions shift with activation state and RNA context. The functional tests around UPF1 and GIGYF1/2 point to biological relevance. That said, some statements could be qualified. The statement that ZFP36L1 "coordinates" multiple pathways implies mechanism and directionality that proximity data alone cannot prove. I suggest reframing as "positions ZFP36L1 within" or "supports a model where ZFP36L1 sits within" these networks.

We thank this reviewer for considering our data ‘directionally convincing, and robust, adding new plausible candidates as interactors with ZFP36L1’. We agree that the proposed wording is more appropriate and will change it accordingly.

2) UPF1, as an upstream regulator of ZFP36L1 expression, is a promising lead. The reduction of ZFP36L1 protein and mRNA in UPF1 knockout, the non-rescue by MG132, and the UPF1 RIP on ZFP36L1 mRNA together argue that UPF1 influences ZFP36L1 transcript output or processing. This claim would read stronger with one short rescue or perturbation that pins the mechanism. A compact test would be UPF1 re-expression in UPF1-deficient T cells with wild-type and helicase-dead alleles. This is realistic in primary T cells using mRNA electroporation or virus-based systems. Approximate time 2 to 3 weeks, including guide design check and expansion. Reagents and sequencing about 2 to 4k USD depending on donor numbers. This would help separate viability or stress effects from a direct role in ZFP36L1 mRNA handling.

We agree that a rescue experiment with wild-type and helicase-dead UPF1 in UPF1-deficient primary T cells would be interesting. Unfortunately, however, UPF1 knockout T cells are less viable and divide less (Supp Figure 6B), making further manipulations such as re-expression by viral transduction technically impossible. We will clarify this limitation in the Discussion and will more explicitly indicate that UPF1 promotes ZFP36L1 mRNA and protein expression, while acknowledging that the precise mechanistic contribution of UPF1 (e.g. to transcript processing, export, or surveillance) remain to be fully resolved.

3) The inference that ZFP36L1 proximity to decapping and deadenylation complexes reflects pathway engagement is reasonable and, frankly, expected. Still, where the manuscript moves from proximity to function, the narrative works best when supported by orthogonal validation. Two compact additions would raise confidence without opening new lines of work. First, a small set of reciprocal co-IPs for PATL1 or DDX6 at endogenous levels in activated T cells, run with and without RNase, would tie the RNase-class assignments to biochemistry. Second, a short-pulse proximity experiment using a reduced biotin dose and shorter labeling window in activated cells would address whether long incubations drive non-specific labeling. Both are feasible in 2 to 3 weeks with minimal extra cost for antibodies and MS runs if the facility is in-house.

We fully agree with the reviewer that orthogonal biochemical validation is valuable. Therefore, we already combined time-resolved proximity labeling (between 0-2h, 2-5h, and 5-16 hours) with time-resolved ZFP36L1 co-IPs ± RNase, to address the dynamic behavior and potential temporal broadening of the interactome.

As to running reciprocal co-IPs for PATL1 or DDX6: we had in fact already considered to follow up on PATL1. However, we failed to identified specific antibodies, revealing many unspecific bands (see below). As to DDX6, antibodies suitable for IP have been reported, and we can therefore offer such reciprocal IP as requested.

To further address the raised points, we will (i) clarify how we define and interpret RNase-sensitive versus RNase-resistant classes (ii) emphasize that some key factors (including PATL1) are already detected in shorter labeling conditions (2 h) in activated T cells (Fig 4C); and (iii) better highlight that the our data provide strong candidates and pathway hypotheses that warrant further mechanistic experimentation in follow-up studies, when moving from proximity to function.

As to the suggested lowering dose of biotin: As described in Figure S1, this appeared unsuccessful. We owe it to the reported dependence and use of biotin in primary T cells (Ref’s 31-33 of this manuscript). This also included that we could not culture T cells in biotin-free medium prior to labeling, as most protocols would do in cell lines.

The reviewer also suggested shorter labeling times. Please be advised that the labeling times chosen were based on the reported protein induction and activity on target mRNAs: 1) ZFP36L1 expression peaks at 2h of T cell activation (Zandhuis et al. 2025; 0.1002/eji.202451641, Petkau et al. 2024; 10.1002/eji.202350700), 3) shows the strongest effects on T cell function between 4-5h, and displays a late phase of activity at 5-16h (Popovic et al. Cell Reports 2023; 10.1016/j.celrep.2023.112419). We realize that additional explanation is warranted for this rationale, which we will provide.

4) Reproducibility is helped by donor pooling, repeated T-cell screens, Jurkat confirmation, and detailed methods including MaxQuant, LIMMA, and supervised patterning. Deposition of MS data is listed. The authors should consider adding a brief, stand-alone analysis notebook in SI or on GitHub with exact filtering thresholds and "shape" definitions, since the supervised profiles are central to claims. This would let others reproduce figures from raw tables with the same code and workflows.

We thank the reviewer for his or her suggestion and we have done as suggested. We will include the following link in the manuscript: https://github.com/ajhoogendijk/ZFP36L1_UltraID

5) Replication and statistics are mostly adequate for discovery proteomics. The thresholds are clear, and PCA and correlation frameworks are appropriate. For functional readouts in edited T cells, please make the number of donors and independent experiments explicit in figure legends, and indicate whether statistics are paired by donor. Where viability differs (UPF1), note any gating strategies used to avoid bias in puromycin or activation marker measurements. These clarifications are quick to add.

Please be advised that the current figure legends already contain the requested information at the bottom (which test used, donor number etc). To highlight this better, we will indicate this point more explicitly in the methods section.

Minor comments 6) The UltraID optimization in primary T cells is useful, but the long 16-hour labeling and high biotin should be framed as a compromise rather than a standard. A short statement about potential off-target labeling during extended incubations would set expectations and justify the RNase and time-course controls.

Please be advised that 1) high biotin was required because primary T cells depend on biotin and 2) increase biotin absorption a 2-7-fold upon activation (Ref 31-33 from the paper). For better time resolution, we included a labeling of 2h (from 0-2h of activation), 3h (from 2-5h) and 9h (from 5-16h) of T cell activation. Nevertheless, we agree that we cannot exclude the risk of off-target labeling, which in fact is inherent to any labeling and pulldown method. We will include such statement in the discussion.

7) The overlap across T-cell screens and with HEK293T APEX datasets is discussed, but a compact quantitative reconciliation would help. A table that lists shared versus cell-type-specific interactors with brief notes on known expression patterns would make this point concrete.

We thank the reviewer for this suggestion. We agree and we will include such table.

8) Figures are generally clear. Where proximity and total proteome PCA are shown, consider adding sample-wise annotations for donor pools and activation time to help readers link variance to biology. Ensure all volcano plots and heatmaps display the exact cutoffs used in text.

We agree that sample-wise annotations would be a nice addition. However, when testing this for e.g. FIgure 1D&E, such differentiation into individual donors becomes illegible due to the many different variables already present. We therefore decided against it.

9) Prior work on ZFP36 family roles in decay, deadenylation via CCR4-NOT, granules, and translational control is cited within the manuscript. In a few places, recent proximity and interactome papers could be more explicitly integrated when comparing overlap, especially where conclusions differ by cell type. A concise paragraph in Discussion that lays out what is truly new in primary T cells would help clarify the contribution of this work to the field.

We appreciate this suggestion and will revise the Discussion accordingly. As to what is new in primary T cells, we would also like to mention that adding H2O2 (required for APEX labeling) to T cells results in immediate cell death can therefore not be employed on T cells. This technical limitation further underscores the valuable contribution of the UltraID-based approach we present here.

Reviewer #1 (Significance (Required)):

Nature and type of advance. The study is a technical and contextual advance in mapping ZFP36L1 proximity partners directly in human primary T cells during activation. The combination of time-resolved labeling and RNase-class assignments is informative. The CRIS PR perturbations provide an initial functional bridge from proximity to phenotype, especially for UPF1.

Context in the literature. ZFP36 family proteins have long been linked to ARE-mediated decay, CCR4-NOT recruitment, and granule localization. The present work confirms those cores and extends them to include decapping and GIGYF1/2-4EHP scaffolds in primary T cells with temporal resolution. The UPF1 link to ZFP36L1 expression adds a plausible surveillance angle that merits follow-up. The cell-type specificity analysis versus HEK293T underscores that proximity networks vary with context.

Audience. Readers in RNA biology, T-cell biology, and proteomics will find the dataset valuable. Groups studying post-transcriptional regulation in immunity can use the resource to prioritize candidate nodes for mechanistic work.

Expertise and scope. I work on post-transcriptional regulation, RNA-protein complexes, and T-cell effector biology. I am comfortable evaluating the conceptual claims, experimental design, and statistical treatment. I am not a mass spectrometry specialist, so I rely on the presented parameters and deposited data for MS acquisition specifics.

To conclude, the manuscript delivers a substantive proximity map of ZFP36L1 in human T cells, with useful temporal and RNA-class information. The UPF1 observations are promising and would benefit from a compact rescue to secure causality. A few minor additions for biochemical validation and transparency in replication would further strengthen the paper.

We thank the reviewer for this comprehensive and constructive assessment. We agree that our study primarily provides a substantive and well-annotated proximity map of ZFP36L1 in human T cells, including temporal and RNA-class information, and that the UPF1 observations constitute a promising lead that merits more detailed mechanistic analysis in follow-up studies.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): The manuscript by Wolkers and colleagues describes the protein interactome of the RNA-binding protein ZFP36L1 in primary human T-cells. There is inherent value in the use of primary cells of human origin, but there is also value in that the study is quite complete, as it is performed in a variety of conditions: T-cells that have been activated or not, at different time points after activation, and by two methods (co-IP and proximity labeling). One might imagine that this basically covers all what can be detected for this protein in T-cells. The authors report a large amount of new interactors involved at all steps in post-transcriptional regulation. In addition, the authors show that UPF1, a known interactor of ZFP36L1, actually binds to ZFP36L1 mRNA and enhances its levels. In sum, the work provides a valuable resource of ZFP36L1 interactors. Yet, how the data add to the mechanistic understanding of ZFP36L1 functions and/or regulation of ZFP36L1 remains unclear.

We thank the reviewer for this enthusiasm on our experimental setups, considering the use of primary T cells of inherent value and our study with the variety of conditions complete.

Major comments: 1) Fig 2: It is confusing that the Pearson correlation to define ZFP36L1 interactors is changed depending on figure panel. In panels A-C, a correlation {greater than or equal to} 0.6 is used, while panel D uses a correlation > 0.5, which changes the nº of interactors. Then, this is changed again in Fig 3A for some cell types but not for others. Why has this been done? It would be better to stick to the same thresholds throughout the manuscript.

Please be advised that different correlation thresholds arise from the composition of the individual datasets: they in depth, number of controls, and the overall dynamic range. The initial proximity labeling experiment (Figure 2A–C) had a higher depth and a larger number of suitable control samples, which allowed us to apply a stricter cutoff (r ≥ 0.6). The time-course experiment and some of the cross-cell-type comparisons have fewer controls and somewhat lower depth, which then required a more permissive threshold (e.g. r > 0.5) to retain known core interactors.

We fully agree that this rationale needs to be explicit. In the revised manuscript we (i) clearly state for each dataset which correlation cutoff is used (ii) emphasize that these thresholds are somewhat arbitrary and should not be directly compared across experiments, and (iii) highlight that our key biological conclusions do not depend on the exact boundary chosen but rather on the consistent enrichment of core complexes and pathways across .

2) Fig 3A: It would be nice to have the information of this Figure panel as a Table (protein name, molecular process(es), known or novel, previously detected in which cells) in addition to the figure.

We agree that this would increase the value of our work as a resource to the community, and we will include such table and merge it with the table Reviewer 1 asked about.

3) Fig 6: To what extent are the effects of UPF1 and GIGFYF1 knock-out on translation and T-cell hyper-activation mediated by ZFP36L1? If deletion of ZFP36L1 itself has no effect on these processes, it seems unlikely that it is involved. In this respect, I am not sure that Fig 6 contributes to the understanding of ZFP36L.

We appreciate this conceptual question. In our dataset, ZFP36L1 knockout affects T-cell activation markers, but does not recapitulate the increased global translation observed upon UPF1 or GIGYF1/2 deletion. We will discuss this finding more explicitly in the Results and Discussion. We discuss the possibility that other ZFP36 family members (e.g. ZFP36/TTP, ZFP36L2) may partially compensate for the absence of ZFP36L1 in some readouts1. Moreover, we will emphasize that at this point it is not clear whether ZFP36L1’s contribution to UPF1 and GIGYF1 protein levels is direct or indirect.

We nonetheless consider Fig. 6 an important component of the story, as it demonstrates that proximity partners emerging from the interactome (UPF1, GIGYF1/2) have measurable functional consequences on T cell activation and translational control, thereby illustrating how the resource can guide mechanistic hypotheses. We will now more carefully phrase this as “first indications of mechanism” and avoid implying that these phenotypes are mediated exclusively via ZFP36L1.

4) Fig 7E: Differences in ZFP36L1 mRNA expression are claimed as a consequence of UPF1 deletion, and indeed there is a clear tendency to reduction of ZFP36L1 mRNA levels upon UPF1 KO. Yet the difference is statistically non-significant. Please, repeat this experiment to increase statistical significance. In addition, a clear discussion on how UPF1 -generally associated to mRNA degradation- contributes to increase ZFP36L1 mRNA levels would be appreciated.

We would like to refrain from including repeats for increasing statistical power. We find similar trends with n=3 at 0h as with n=7 at 3h of activation (Fig. 7E). We rather would like to stress that despite the width overall expression levels which most probably stems from using primary human material, the overall levels of ZFP36L1 mRNA are lower in UPF1 KO T cells. We will include a point on how UPF1 possibly may contribute to the decreased ZFP36L1 mRNA levels, as suggested.

5) Fig 6A: The decrease in global translation by GIGFYF1 knock-out upon activation claimed by the authors is not clear in Fig 6A and is non-significant upon quantification. Please, modify narrative accordingly.

Indeed, this was not phrased well. We will correct our description to match the statistical analysis.

6) Page 6: The authors state 'This included the PAN2/3 complex proteins which trim poly(A) tails prior to mRNA degradation through the CCR4/NOT complex'. To the best of my knowledge, the CCR4/NOT complex does not degrade the body of the mRNA. Both PAN2/3 and CCR4/NOT are deadenylases that function independently.

We thank the reviewer for highlighting this inaccuracy. PAN2/3 and CCR4–NOT are indeed both deadenylase complexes that function independently rather than one acting strictly upstream of the other in degrading the mRNA body. We will correct this statement to that PAN2/3 and CCR4–NOT cooperate in poly(A) tail shortening and do not themselves degrade the mRNA body, which is instead handled by the downstream decay machinery.

7) Please, label all Table sheets. Right now one has to guess what is being shown in most of them. Furthermore, it would be convenient to join all Tables related to the same Figure in one unique Excel with several sheets, rather than having many Tables with only one sheet each.

We appreciate this suggestion. In the revised supplementary files all table sheets will be clearly labeled to indicate the corresponding figure and dataset, and combined into a single excel file when multiple tables relate to the same figure. We have already done so.

Minor comments: 8) Fig 1E: Shouldn't there be a better separation by biotinylation in the UltraID IP principal component analysis? In theory, only biotinylated proteins should be immunoprecipitated.

In theory this should indeed be the case. However, in practice, pull down experiments always suffer from background stickiness of proteins to tubes, beads etc. Combined, these known background issues highlight the critical addition of control samples, allowing for unequivocal call of proteins that are above background.

In addition, as we indicated in the manuscript, primary T cells depend on Biotin. This prohibited us to use biotin-free medium, even for a short culture period (it resulted in cell death). Such biotin-free culture steps are included in proximity labeling assays performed in cell lines. Owing to the continuous addition of biotin, some of the ‘background’ biotinylation signal may even be ‘real’. Nevertheless, the higher levels of biotin we added during the labeling results in increased signals, and statistical analysis with these controls identifies which of the proteins are above background, irrespective from the source. We will include a short note on this in the manuscript

9) Fig 3B-E: Is the labeling not swapped, top (always +) is Biotin and bottom (- or +) is aCD3/aCD28?

We thank the reviewer for catching this mistake- we have corrected it

10) Fig 7A data is from another paper, so I suggest to move this panel to Supplementary materials.

We respectfully disagree. Please be advised that we reanalysed data from published datasets, that resulted in this figure. Re-analysis is a widely accepted method and certainly used for main figure panels. Our re-analysis from Bestenhorn et al 2025; (10.1016/j.molcel.2025.01.001) confirms that ZFP36L1 interacts with UPF1 and GIGYF1/2 in the RAW 264.7 macrophage cell line, which we consider an important consolidation of our findings. To highlight that this table is a re-analysis of published data, we will include this information (including the reference) below the data. As ‘extracted from Bestenhorn et al'

11) Fig S1A: Why is there so much labeling in the UltraID only lane without biotin?

This is a phenomenon also reported by others (Kubitz et al. 2022; 10.1038/s42003-022-03604-5: Figure 5A). UltraID alone is a small protein of (19.7KD), comparable to TurboID or others (Kubitz et al. 2022; 10.1038/s42003-022-03604-5). If not tethered to a specific compartment, these proximity labeling moieties can diffuse through the cytoplasm, biotinylating any protein they ‘bump’ into. Please be advised that we included this control to show this effect, to substantiate why we use GFP-UltraID- as control, to limit such background effects. To highlight this point better, we will better articulate this reasoning in the results section.

12) Fig S1E: Please, explain better. What is WT?

We thank the reviewer for catching this inconsistency. We will explicitly define “WT” as wild-type primary T cells (non-edited, non-transduced) and clarify how this relates to the other conditions.

13) Fig S4B: Please, explain the labels on top of the shapes.

We will update the figure, explaining how the labels above each shape are chosen (e.g. indicating specific clusters, functional categories, or experimental conditions, as appropriate). This should make the reading more intuitive.

14) Page 3: A time-course of incubation with biotin is lacking in Fig S1B, and thereby it is confusing that the authors direct readers to this figure when an increased to 16h incubation is claimed to be better.

Please be advised that short labeling times yielded disappointing results in primary human T cells. Therefore all first analyses were performed with 16h biotinylation, as depicted in Figure S1B). Only after achieving good results (presented in Figure 1B), we performed time course experiments (presented in __Figure 4, __lowering incubation times to 2h, 3h and 9h). We realize that this is confusing and we will rephrase this point in page 3.

Reviewer #2 (Significance (Required)): Strengths: A thorough repository of ZFP36L1 interactors in primary human T-cells. A valuable resource for the community. Weaknesses: There is little mechanistic insight on ZFP36L1 function or regulation.

We would like to highlight that the purpose of our study was to provide a comprehensive interactome of ZFP36L1, and to study the dynamics of these interactions. In addition to known interactors, we identified novel putative interactors of ZFP36L1. We have indeed not followed up on all interactions, which we consider beyond the scope of this manuscript. Rather, we consider our study as a toolbox for the community, that helps in their studies.

Nevertheless, in Fig 6-7, we show first indications of mechanistic insights on ZFP36L1 interactors, exemplifying how the findings of this resource paper can be used by the community.

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

The authors have analyzed the interactome of ZFP36L1 in primary human T cells using a biotin-based proximity labeling method. In addition to proteins that are known to interact with ZFP36L1, the authors defined a multitude of novel interactions involved in mRNA decapping, mRNA degradation pathways, translation repressors, stress granule/p-body formation, and other regulatory pathways. Time-lapse proximity labeling revealed that the ZFP36L1 interactome undergoes remodeling during T cell activation. Co-IP for ZFP36L1 executed in the presence/absence of RNA further revealed the interactome and possible regulators of ZFP36L1, including the helicase UPF1. In addition to interacting with ZFP36L1, UPF1 promotes the ZFP36L1 protein expression, seemingly by binding to the ZFP36L1 mRNA transcript, and in some way stabilizing it. This comprehensive interactome map highlights the widespread interactions of ZFP36L1 with proteins of many types, and its potential roles in diverse T cell processes. Although somewhat descriptive, rather than hypothesis-testing, this work represents an important contribution to understanding the potential roles of the ZFP36 family proteins, and sets up many future experiments which could test molecular details.

We thank the reviewer for these thoughtful points, and for recognizing our paper as an important contribution for the field as resource, that should support future experiments.

Major points: 1) Can the authors discuss the specificity of the antibody for ZFP36L1 used in the Co-IP experiments? The antibody listed in Appendix A is abcam catalog number ab42473, although the catalog number for this antibody (unlike the others major ones used) is not listed in the Methods section - please add this to the Methods to make it easier for readers to find this detail. Could this antibody also be immunoprecipitating ZFP36 or ZFP36L2? Other antibodies have had cross-reactivity for the different family members. It is also notable that this antibody has been discontinued by the manufacturer (https://www.abcam.com/en-us/products/unavailable/zfp36l1-antibody-ab42473). Have the authors tried the current abcam anti-ZFP36L1 antibody being sold, catalog number ab230507?

We appreciate the opportunity to clarify this important technical point. We have now added the catalog number (ab42473, Abcam) of the anti-ZFP36L1 antibody used for co-IP to the Methods section, in addition to Appendix A, to facilitate reproducibility. The antibody ab42473 has indeed been discontinued by the manufacturer. We have contacted the manufacturer on multiple occasions with no luck.

We have evaluated multiple alternative anti-ZFP36L1 antibodies, including the currently available Abcam antibody ab230507. In our hands, these alternatives showed weaker or less specific detection of ZFP36L1 compared to the original ZFP36L1 antibody. Only antibody 1A3 recognized ZFP36L1. We therefore used this antibody for the Co-IP. Importantly, even though the signal is lower than the original antibody we used, the migration patterns observed with ab42473 in our co-IP experiments match the expected molecular weight of ZFP36L1 and do not suggest substantial cross-reactivity with ZFP36 or ZFP36L2, which display distinct sizes (we will add the sizes to the WB in figures). We discuss this point briefly in the revised Methods/Results.

2) On this point, the authors report interactions between ZFP36L1 and its related proteins ZFP36 and ZFP36L2 in the Co-IP experiment (Supp 5C). Did these proteins interact in the proximity labeling? Ideally this could be discussed in the Discussion section.

ZFP36 and ZFP36L2 were indeed detected as co-precipitating with ZFP36L1 in the co-IP experiments but were not found as high-confidence interactors in the UltraID proximity labeling datasets. Also in the APEX proximity labeling of Bestehorn et al. In RAW macrophage cells, they did not find ZFP36 or ZFP36L1 to interact with ZFP36L1. * *We now explicitly mention this in the Results and discuss it in the Discussion.

3) Can the authors discuss more fully the limited overlap in identified interactors across the two proximity labeling screens performed in primary T cells (Fig 2C)? Likewise, can the authors comment on the very limited overlap between the screens in T cells and the published ZFP36L1-APEX proximity labelling experiment performed in the HEK293T cell line by Bestehorn et al. (ref 42)? Only 6.8% of proteins found in either T cell screen were found as interactors in this cell line. The authors comment that this may be because "...either expression of certain proteins is cell-type specific, or [because] ZFP36L1 has cell-type specific protein interactions, in addition to its core interactome". While I agree that cell-type specific interactions may be at play, I would think most of the interactors found in the T cell screens are widely expressed proteins necessary for central cell functions.

First, the apparent overlap percentage depends on depth and filtering. As noted above and now detailed in a new Supplementary table, a core set of decapping, deadenylation, and granule-associated factors is consistently recovered across our T-cell screens and the HEK293T APEX dataset. However, beyond this core protein, overlap is reduced, reflecting several factors: (i) differences in expression levels of many interactors between HEK293T cells and primary T cells; (ii) the activation-dependent nature of ZFP36L1 function in T cells, which cannot be fully mimicked in HEK293T; (iii) different proximity labeling enzymes and fusion constructs (APEX vs UltraID, different tags, expression levels); and (iv) distinct experimental designs and control strategies, which influence statistical filtering and the effective “depth” of each interactome.

In the revised Discussion and in the new comparative table, we now emphasize that while many of the ZFP36L1 proximity partners identified in T cells are indeed widely expressed, their effective labeling and enrichment are strongly context dependent. We therefore interpret the relatively limited overlap as highlighting both a robust core interactome and substantial context-specific remodeling, rather than as evidence of artifacts in one or the other dataset.

Minor comments: 4) In Figure 3D, the legend states that black circles indicate significantly enriched proteins in biotin samples, while grey circles indicate non-significant enrichment. However, some genes, including DCP1A, DDX6, YBX1, have black circles in the -biotin group and grey in the +biotin group, which creates confusion in interpretation.

We thank the reviewer for this comment. We have accidentally switched the labeling of biotin and activation as pointed out by reviewer 2. Once this is fixed, this comment will also be fixed.

5) Did the authors find any interactors whose expression is known to be specific to CD4 or CD8 T cells?

In our current dataset we did not identify interactors whose presence was clearly restricted to CD4 or CD8 T-cells. We agree that differential ZFP36L1 interactomes in defined T-cell subsets represent an interesting avenue for future targeted studies and will outline this is the discussion.

Reviewer #3 (Significance (Required)):

The authors present the first comprehensive analysis of the ZFP36L1 interactome in primary T cells. The use of biotin-based proximity labeling enables detection of physiologically relevant interactions in live cells. This approach revealed many novel interactors.

Strengths include the overall richness of the dataset, and the hypothesis-provoking experiments that could follow in the future. Limitations include somewhat limited overlap with a published proximity labeling dataset from performed in a different cell line, suggesting that there may be artifacts in one or both datasets.

The audience for this article would include those interested broadly in RNA binding proteins and those interested in post-transcriptional and translational regulation.

I have immunology expertise on T cell activation and differentiation and expertise on transcriptional and post-transcriptional regulation of gene expression in T cells.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

This paper presents a computational model of the evolution of two different kinds of helping ("work," presumably denoting provisioning, and defense tasks) in a model inspired by cooperatively breeding vertebrates. The helpers in this model are a mix of previous offspring of the breeder and floaters that might have joined the group, and can either transition between the tasks as they age or not. The two types of help have differential costs: "work" reduces "dominance value," (DV), a measure of competitiveness for breeding spots, which otherwise goes up linearly with age, but defense reduces survival probability. Both eventually might preclude the helper from becoming a breeder and reproducing. How much the helpers help, and which tasks (and whether they transition or not), as well as their propensity to disperse, are all evolving quantities. The authors consider three main scenarios: one where relatedness emerges from the model, but there is no benefit to living in groups, one where there is no relatedness, but living in larger groups gives a survival benefit (group augmentation, GA), and one where both effects operate. The main claim is that evolving defensive help or division of labor requires the group augmentation; it doesn't evolve through kin selection alone in the authors' simulations.

This is an interesting model, and there is much to like about the complexity that is built in. Individual-based simulations like this can be a valuable tool to explore the complex interaction of life history and social traits. Yet, models like this also have to take care of both being very clear on their construction and exploring how some of the ancillary but potentially consequential assumptions affect the results, including robust exploration of the parameter space. I think the current manuscript falls short in these areas, and therefore, I am not yet convinced of the results. In this round, the authors provided some clarity, but some questions still remain, and I remain unconvinced by a main assumption that was not addressed.

Based on the authors' response, if I understand the life history correctly, dispersers either immediately join another group (with 1-the probability of dispersing), or remain floaters until they successfully compete for a breeder spot or die? Is that correct? I honestly cannot decide because this seems implicit in the first response but the response to my second point raises the possibility of not working while floating but can work if they later join a group as a subordinate. If it is the case that floaters can have multiple opportunities to join groups as subordinates (not as breeders; I assume that this is the case for breeding competition), this should be stated, and more details about how. So there is still some clarification to be done, and more to the point, the clarification that happened only happened in the response. The authors should add these details to the main text. Currently, the main text only says vaguely that joining a group after dispersing " is also controlled by the same genetic dispersal predisposition" without saying how.

In each breeding cycle, individuals have the opportunity to become a breeder, a helper, or a floater. Social role is really just a state, and that state can change in each breeding cycle (see Figure 1). Therefore, floaters may join a group as subordinates at any point in time depending on their dispersal propensity, and subordinates may also disperse from their natal group any given time. In the “Dominance-dependent dispersal propensities” section in the SI, this dispersal or philopatric tendency varies with dominance rank.

We have added: “In each breeding cycle” (L415) to clarify this further.

In response to my query about the reasonableness of the assumption that floaters are in better condition (in the KS treatment) because they don't do any work, the authors have done some additional modeling but I fail to see how that addresses my point. The additional simulations do not touch the feature I was commenting on, and arguably make it stronger (since assuming a positive beta_r -which btw is listed as 0 in Table 1- would make floaters on average be even more stronger than subordinates). It also again confuses me with regard to the previous point, since it implies that now dispersal is also potentially a lifetime event. Is that true?

We are not quite sure where the reviewer gets this idea because we have never assumed a competitive advantage of floaters versus helpers. As stated in the previous revision, floaters can potentially outcompete subordinates of the same age if they attempt to breed without first queuing as a subordinate (step 5 in Figure 1) if subordinates are engaged in work tasks. However, floaters also have higher mortality rates than group members, which makes them have lower age averages. In addition, helpers have the advantage of always competing for an open breeding position in the group, while floaters do not have this preferential access (in Figure S2 we reduce even further the likelihood of a floater to try to compete for a breeding position).

Moreover, in the previous revision (section: “Dominance-dependent dispersal propensities” in the SI) we specifically addressed this concern by adding the possibility that individuals, either floaters or subordinate group members, react to their rank or dominance value to decide whether to disperse (if subordinate) or join a group (if floater). Hence, individuals may choose to disperse when low ranked and then remain on the territory they dispersed to as helpers, OR they may remain as helpers in their natal territory as low ranked individuals and then disperse later when they attain a higher dominance value. The new implementation, therefore, allows individuals to choose when to become floaters or helpers depending on their dominance value. This change to the model affects the relative competitiveness between floaters and helpers, which avoids the assumption that either low- or high-quality individuals are the dispersing phenotype and, instead, allows rank-based dispersal as an emergent trait. As shown in Figure S5, this change had no qualitative impact on the results.

To make this all clearer, we have now added to all of the relevant SI tables a new row with the relative rank of helpers vs floaters. As shown, floaters do not consistently outrank helpers. Rather, which role is most dominant depends on the environment and fitness trade-offs that shape their dispersing and helping decisions.

Some further clarifications: beta_r is a gene that may evolve either positive or negative values, 0 (no reaction norm of dispersal to dominance rank) is the initial value in the simulations before evolution takes place. Therefore, this value may evolve to positive or negative values depending on evolutionary trade-offs. Also, and as clarified in the previous comment, the decision to disperse or not occurs at each breeding cycle, so becoming a floater, for example, is not a lifetime event unless they evolve a fixed strategy (dispersal = 0 or 1). 

Meanwhile, the simplest and most convincing robustness check, which I had suggested last round, is not done: simply reduce the increase in the R of the floater by age relative to subordinates. I suspect this will actually change the results. It seems fairly transparent to me that an average floater in the KS scenario will have R about 15-20% higher than the subordinates (given no defense evolves, y_h=0.1 and H_work evolves to be around 5, and the average lifespan for both floaters and subordinates are in the range of 3.7-2.5 roughly, depending on m). That could be a substantial advantage in competition for breeding spots, depending on how that scramble competition actually works. I asked about this function in the last round (how non-linear is it?) but the authors seem to have neglected to answer.

As we mentioned in the previous comment above, we have now added the relative rank between helpers and floaters to all the relevant SI tables, to provide a better idea of the relative competitiveness of residents versus dispersers for each parameter combination. As seen in Table S1, the competitive advantage of floaters is only marginally in the favor for floaters in the “Only kin selection” implementation. This advantage only becomes more pronounced when individuals can choose whether to disperse or remain philopatric depending on their rank. In this case, the difference in rank between helpers and floaters is driven by the high levels of dispersal, with only a few newborns (low rank) remaining briefly in the natal territory (Table S6). Instead, the high dispersal rates observed under the “Only kin selection” scenario appear to result from the low incentives to remain in the group when direct fitness benefits are absent, unless indirect fitness benefits are substantially increased. This effect is reinforced by the need for task partitioning to occur in an all-or-nothing manner (see the new implementation added to the “Kin selection and the evolution of division of labor” in the Supplementary materials; more details in following comments).

In addition, we specifically chose not to impose this constraint of forcing floaters to be lower rank than helpers because doing so would require strong assumptions on how the floaters rank is determined. These assumptions are unlikely to be universally valid across natural populations (and probably not commonly met in most species) and could vary considerably among species. Therefore, it would add complexity to the model while reducing generalizability.

As stated in the previous revision, no scramble competition takes place, this was an implementation not included in the final version of the manuscript in which age did not have an influence in dominance. Results were equivalent and we decided to remove it for simplicity prior to the original submission, as the model is already very complex in the current stage; we simply forgot to remove it from Table 1, something we explained in the previous round of revisions.

More generally, I find that the assumption (and it is an assumption) floaters are better off than subordinates in a territory to be still questionable. There is no attempt to justify this with any data, and any data I can find points the other way (though typically they compare breeders and floaters, e.g.: https://bioone.org/journals/ardeola/volume-63/issue-1/arla.63.1.2016.rp3/The-Unknown-Life-of-Floaters--The-Hidden-Face-of/10.13157/arla.63.1.2016.rp3.full concludes "the current preliminary consensus is that floaters are 'making the best of a bad job'."). I think if the authors really want to assume that floaters have higher dominance than subordinates, they should justify it. This is driving at least one and possibly most of the key results, since it affects the reproductive value of subordinates (and therefore the costs of helping).

We explicitly addressed this in the previous revision in a long response about resource holding potential (RHP). Once again, we do NOT assume that dispersers are at a competitive advantage to anyone else. Floaters lack access to a territory unless they either disperse into an established group or colonize an unoccupied territory. Therefore, floaters endure higher mortalities due to the lack of access to territories and group living benefits in the model, and are not always able to try to compete for a breeding position.

The literature reports mixed evidence regarding the quality of dispersing individuals, with some studies identifying them as low-quality and others as high-quality, attributing this to them experiencing fewer constraints when dispersing that their counterparts (e.g. Stiver et al. 2007 Molecular Ecology; Torrents‐Ticó, et al. 2018 Journal of Zoology). Additionally, dispersal can provide end-of-queue individuals in their natal group an opportunity to join a queue elsewhere that offers better prospects, outcompeting current group members (Nelson‐Flower et al. 2018 Journal of Animal Ecology). Moreover, in our model floaters do not consistently have lower dominance values or ranks than helpers, and dominance value is often only marginally different.

In short, we previously addressed the concern regarding the relative competitiveness of floaters compared to subordinate group members. To further clarify this point here, we have now included additional data on relative rank in all of the relevant SI tables. We hope that these additions will help alleviate any remaining concerns on this matter.

Regarding division of labor, I think I was not clear so will try again. The authors assume that the group reproduction is 1+H_total/(1+H_total), where H_total is the sum of all the defense and work help, but with the proviso that if one of the totals is higher than "H_max", the average of the two totals (plus k_m, but that's set to a low value, so we can ignore it), it is replaced by that. That means, for example, if total "work" help is 10 and "defense" help is 0, total help is given by 5 (well, 5.1 but will ignore k_m). That's what I meant by "marginal benefit of help is only reduced by a half" last round, since in this scenario, adding 1 to work help would make total help go to 5.5 vs. adding 1 to defense help which would make it go to 6. That is a pretty weak form of modeling "both types of tasks are necessary to successfully produce offspring" as the newly added passage says (which I agree with), since if you were getting no defense by a lot of food, adding more food should plausibly have no effect on your production whatsoever (not just half of adding a little defense). This probably explains why often the "division of labor" condition isn't that different than the no DoL condition.

The model incorporates division of labor as the optimal strategy for maximizing breeder productivity, while penalizing helping efforts that are limited to either work or defense alone. Because the model does not intend to force the evolution of help as an obligatory trait (breeders may still reproduce in the absence of help; k₀ ≠ 0), we assume that the performance of both types of task by the helpers is a non-obligatory trait that complements parental care.

That said, we recognize the reviewer’s concern that the selective forces modeled for division of labor might not be sufficient in the current simulations. To address this, we have now introduced a new implementation, as discussed in the “Kin selection and the evolution of division of labor” section in the SI. In this implementation, division of labor becomes obligatory for breeders to gain a productivity boost from the help of subordinate group members. The new implementation tests whether division of labor can arise solely from kin selection benefits. Under these premises, philopatry and division of labor do emerge through kin selection, but only when there is a tenfold increase in productivity per unit of help compared to the default implementation. Thus, even if such increases are biologically plausible, they are more likely to reflect the magnitudes characteristic of eusocial insects rather than of cooperatively breeding vertebrates (the primary focus of this model). Such extreme requirements for productivity gains and need for coordination further suggest that group augmentation, and not kin selection, is probably the primary driving force particularly in harsh environments. This is now discussed in L210-213.

Reviewer #2 (Public review):

Summary:

This paper formulates an individual-based model to understand the evolution of division of labor in vertebrates. The model considers a population subdivided in groups, each group has a single asexually-reproducing breeder, other group members (subordinates) can perform two types of tasks called "work" or "defense", individuals have different ages, individuals can disperse between groups, each individual has a dominance rank that increases with age, and upon death of the breeder a new breeder is chosen among group members depending on their dominance. "Workers" pay a reproduction cost by having their dominance decreased, and "defenders" pay a survival cost. Every group member receives a survival benefit with increasing group size. There are 6 genetic traits, each controlled by a single locus, that control propensities to help and disperse, and how task choice and dispersal relate to dominance. To study the effect of group augmentation without kin selection, the authors cross-foster individuals to eliminate relatedness. The paper allows for the evolution of the 6 genetic traits under some different parameter values to study the conditions under which division of labour evolves, defined as the occurrence of different subordinates performing "work" and "defense" tasks. The authors envision the model as one of vertebrate division of labor.

The main conclusion of the paper is that group augmentation is the primary factor causing the evolution of vertebrate division of labor, rather than kin selection. This conclusion is drawn because, for the parameter values considered, when the benefit of group augmentation is set to zero, no division of labor evolves and all subordinates perform "work" tasks but no "defense" tasks.

Strengths:

The model incorporates various biologically realistic details, including the possibility to evolve age polytheism where individuals switch from "work" to "defence" tasks as they age or vice versa, as well as the possibility of comparing the action of group augmentation alone with that of kin selection alone.

Weaknesses:

The model and its analysis is limited, which makes the results insufficient to reach the main conclusion that group augmentation and not kin selection is the primary cause of the evolution of vertebrate division of labor. There are several reasons.

First, the model strongly restricts the possibility that kin selection is relevant. The two tasks considered essentially differ only by whether they are costly for reproduction or survival. "Work" tasks are those costly for reproduction and "defense" tasks are those costly for survival. The two tasks provide the same benefits for reproduction (eqs. 4, 5) and survival (through group augmentation, eq. 3.1). So, whether one, the other, or both tasks evolve presumably only depends on which task is less costly, not really on which benefits it provides. As the two tasks give the same benefits, there is no possibility that the two tasks act synergistically, where performing one task increases a benefit (e.g., increasing someone's survival) that is going to be compounded by someone else performing the other task (e.g., increasing that someone's reproduction). So, there is very little scope for kin selection to cause the evolution of labour in this model. Note synergy between tasks is not something unusual in division of labour models, but is in fact a basic element in them, so excluding it from the start in the model and then making general claims about division of labour is unwarranted. I made this same point in my first review, although phrased differently, but it was left unaddressed.

The scope of this paper was to study division of labor in cooperatively breeding species with fertile workers, in which help is exclusively directed towards breeders to enhance offspring production (i.e., alloparental care), as we stated in the previous review. Therefore, in this context, helpers may only obtain fitness benefits directly or indirectly by increasing the productivity of the breeders. This benefit is maximized when division of labor occurs between group members as there is a higher return for the least amount of effort per capita. Our focus is in line with previous work in most other social animals, including eusocial insects and humans, which emphasizes how division of labor maximizes group productivity. This is not to suggest that the model does not favor synergy, as engaging in two distinct tasks enhances the breeders' productivity more than if group members were to perform only one type of alloparental care task. We have expanded on the need for division of labor by making the performance of each type of task a requirement to boost the breeders productivity, see more details in a following comment.

Second, the parameter space is very little explored. This is generally an issue when trying to make general claims from an individual-based model where only a very narrow parameter region has been explored of a necessarily particular model. However, in this paper, the issue is more evident. As in this model the two tasks ultimately only differ by their costs, the parameter values specifying their costs should be varied to determine their effects. Instead, the model sets a very low survival cost for work (yh=0.1) and a very high survival cost for defense (xh=3), the latter of which can be compensated by the benefit of group augmentation (xn=3). Some very limited variation of xh and xn is explored, always for very high values, effectively making defense unevolvable except if there is group augmentation. Hence, as I stated in my previous review, a more extensive parameter exploration addressing this should be included, but this has not been done. Consequently, the main conclusion that "division of labor" needs group augmentation is essentially enforced by the limited parameter exploration, in addition to the first reason above.

We systematically explored the parameter landscape and report in the body of the paper only those ranges that lead to changes in the reaction norms of interest (other ranges are explored in the SI). When looking into the relative magnitude of cost of work and defense tasks, it is important to note that cost values are not directly comparable because they affect different traits. However, the ranges of values capture changes in the reaction norms that lead to rank-depending task specialization.

To illustrate this more clearly, we have added a new section in the SI (Variation in the cost of work tasks instead of defense tasks section) showing variation in y_h, which highlights how individuals trade off the relative costs of different tasks. As shown, the results remain consistent with everything we showed previously: a higher cost of work (high y_h) shifts investment toward defense tasks, while a higher cost of defense (high x_h) shifts investment toward work tasks.

Importantly, additional parameter values were already included in the SI of the previous revision, specifically to favor the evolution of division of labor under only kin selection. Basically, division of labor under only kin selection does happen, but only under conditions that are very restrictive, as discussed in the “Kin selection and the evolution of division of labor” section in the SI. We have tried to make this point clearer now (see comments to previous reviewer above, and to this reviewer right below).

Third, what is called "division of labor" here is an overinterpretation. When the two tasks evolve, what exists in the model is some individuals that do reproduction-costly tasks (so-called "work") and survival-costly tasks (so-called "defense"). However, there are really no two tasks that are being completed, in the sense that completing both tasks (e.g., work and defense) is not necessary to achieve a goal (e.g., reproduction). In this model there is only one task (reproduction, equation 4,5) to which both "tasks" contribute equally and so one task doesn't need to be completed if the other task compensates for it. So, this model does not actually consider division of labor.

Although it is true that we did not make the evolution of help obligatory and, therefore, did not impose division of labor by definition, the assumptions of the model nonetheless create conditions that favor the emergence of division of labor. This is evident when comparing the equilibria between scenarios where division of labor was favored versus not favored (Figure 2 triangles vs circles).

That said, we acknowledge the reviewer’s concern that the selective forces modeled in our simulations may not, on their own, be sufficient to drive the evolution of division of labor under only kin selection. Therefore, we have now added a section where we restrict the evolution of help to instances in which division of labor is necessary to have an impact on the dominant breeder productivity. Under this scenario, we do find division of labor (as well as philopatry) evolving under only kin selection. However, this behavior only evolves when help highly increases the breeders’ productivity (by a factor of 10 what is needed for the evolution of division of labor under group augmentation). Therefore, group augmentation still appears to be the primary driver of division of labor, while kin selection facilitates it and may, under certain restrictive circumstances, also promote division of labor independently (discussed in L210-213).

Reviewer #1 (Recommendations for the authors):

I really think you should do the simulations where floaters do not come out ahead by floating. That will likely change the result, but if it doesn't, you will have a more robust finding. If it does, then you will have understood the problem better.

As we outlined in the previous round of revisions, implementing this change would be challenging without substantially increasing model complexity and reducing its general applicability, as it would require strong assumptions that could heavily influence dispersal decisions. For instance, by how much should helpers outcompete floaters? Would a floater be less competitive than a helper regardless of age, or only if age is equal? If competitiveness depends on equal age, what is the impact of performing work tasks given that workers always outcompete immigrants? Conversely, if floaters are less competitive regardless of age, is it realistic that a young individual would outcompete all immigrants? If a disperser finds a group immediately after dispersal versus floating for a while, is the dominance value reduced less (as would happen to individuals doing prospections before dispersal)? 

Clearly it is not as simple as the referee suggests because there are many scenarios that would need to be considered and many assumptions made in doing this. As we explained to the points above, we think our treatment of floaters is consistent with the definition of floaters in the literature, and our model takes a general approach without making too many assumptions.

Reviewer #2 (Recommendations for the authors):

The paper's presentation is still unclear. A few instances include the following. It is unclear what is plotted in the vertical axes of Figure 2, which is T but T is a function of age t, so this T is presumably being plotted at a specific t but which one it is not said.

The values graphed are the averages of the phenotypically expressed tasks, not the reaction norms per se. We have now rewritten the the axis to “Expressed task allocation T (0 = work, 1 = defense)” to increase clarity across the manuscript.

The section titled "The need for division of labor" in the methods is still very unclear.

We have rephased this whole section to improve clarity.

This work has been published in GigaByte Journal under a CC-BY 4.0 license (https://doi.org/10.46471/gigabyte.168), and has published the reviews under the same license.

Reviewer 1. Haikuo Li

Is there a clear statement of need explaining what problems the software is designed to solve and who the target audience is? No. Should be made more clear.

Comments: The authors developed EMImR as an R toolkit and open-sourced software for analysis of bulk RNA-seq as well as epigenomic sequencing data including DNA methylation seq and non-coding RNA profiling. This work is very interesting and should be of interest to people interested in transcriptomic and epigenomic data analysis but without computational background. I have two major comments: 1. Results presented in this manuscript were only from microarray datasets and are kind of “old” data. Although these data types and sequencing platforms are still very valuable, I don’t think they are widely used as of today, and therefore, it may be less compelling to the audience. It is suggested to validate EMImR using additional more recently published datasets. 2. The authors studied bulk transcriptomic and epigenomic sequencing data. In fact, single-cell and spatially resolved profiling of these modalities are becoming the mainstream of biomedical research since those methods offer much better resolution and biological insights. The authors are encouraged to discuss some key references of this field (for example, PMIDs: 34062119 and 38513647 for single-cell multiomics; PMID: 40119005 for spatial multiomics sequencing), potentially as the future direction of package development. Re-review: The authors have answered my questions and added new content in the Discussion section as suggested.

Reviewer 2. Weiming He

Dear Editor-in-Chief, The EMImR developed by the author is a Shiny application designed for the identification of transcriptomic and epigenomic changes and data association. This program is mainly targeted at Windows UI users who do not possess extensive computational skills. Its core function is to identify the intersections between genetic and epigenetic modifications

Review Recommendation I recommend that after making appropriate revisions to the current “Minor Revision”, the article can be accepted. However, the author needs to address the following issues.

Major Issue The article does not provide specific information on the resource consumption (memory and time) of the program. This is crucial for new users. Although we assume that the resource consumption is minimal, users need to know the machine configuration required to run the program. Therefore, I suggest adding two columns for “Time” and “Memory” in Table 1.

Minor Issues 1. GitHub Page The Table of Contents on the GitHub page provides a Demonstration Video. However, due to restricted access to YouTube in some regions, it is recommended to also upload a manual in PDF format named “EMImR_manual.pdf” on GitHub. In step 4 of the Installation Guide, it states that “All dependencies will be installed automaticly”. It is advisable to add a step: if the installation fails, prompt the user about the specific error location and guide the user to install the dependent packages manually first to ensure successful installation. Currently, the command “source(‘Dependencies_emimr.R’)” does not return any error messages, which is extremely inconvenient for novice users. The author can provide the maintainer's email address so that users can seek timely solutions when encountering problems

1. R Version The author recommends using R - 4.2.1 (2022), which was released three years ago. The current latest version is R 4.5.1. It is suggested that the author test the program with the latest version to ensure its adaptability to future developments.

2. Flowchart Suggestion It is recommended to add a flowchart to illustrate the sequential relationships among packages such as DESeq2 for differential analysis, clusterProfiler for clustering, enrichplot for plotting, and miRNA - related packages (this is optional).

4.Function Addition Currently, the program seems to lack a button for saving PDFs, as well as functions for batch uploading, saving sessions, and one - click exporting of PDF/PNG files. It is recommended to add the “shinysaver” and “downloadHandler” functions to fulfill these requirements.

1. Personalized Features and Upgrade Plan To attract more users, more personalized features should be added. The author can mention the future upgrade plan in the discussion section. For example, currently, DESeq2 is used for differential analysis, and in future upgrades, more methods such as PossionDis, NOIseq, and EBseq could be provided for users to choose from.

2. Text Polishing Suggestions 6.1 Unify the usage of “down - regulated” and “downregulated”, preferably using the latter. 6.2 “R - studio version” ---》 “RStudio” 6.3 Lumian, ---》 Lumian 6.4 no login wall ---》 does not require user registration 6.5 Rewrite “genes were simultaneously differentially expressed and methylated” as “genes that were both differentially expressed and differentially methylated”. 6.6 Ensure that Latin names of species are in italics 6.7 make corresponding modifications to other sentences to improve the accuracy and professionalism of the language in the article.

The above are my detailed review comments on this article. I hope they can provide a reference for your decision - making.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Manuscript number: RC -2025-03175

Corresponding author(s): Gernot Längst

[Please use this template only if the submitted manuscript should be considered by the affiliate journal as a full revision in response to the points raised by the reviewers.

• *

If you wish to submit a preliminary revision with a revision plan, please use our "Revision Plan" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

2. Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

We thank the reviewers for their efforts and detailed evaluation of our manuscript. We think that the comments of the reviewers allowed us to significantly improve the manuscript.

With best regards

The authors of the manuscript

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

Summary: Holzinger et al. present a new automated pipeline, nucDetective, designed to provide accurate nucleosome positioning, fuzziness, and regularity from MNase-seq data. The pipeline is structured around two main workflows-Profiler and Inspector-and can also be applied to time-series datasets. To demonstrate its utility, the authors re-analyzed a Plasmodium falciparum MNase-seq time-series dataset (Kensche et al., 2016), aiming to show that nucDetective can reliably characterize nucleosomes in challenging AT-rich genomes. By integrating additional datasets (ATAC-seq, RNA-seq, ChIP-seq), they argue that the nucleosome positioning results from their pipeline have biological relevance.

Major Comments:

Despite being a useful pipeline, the authors draw conclusions directly from the pipeline's output without integrating necessary quality controls. Some claims either contradict existing literature or rely on misinterpretation or insufficient statistical support. In some instances, the pipeline output does not align with known aspects of Plasmodium biology. I outline below the key concerns and suggested improvements to strengthen the manuscript and validate the pipeline:

Clarification of +1 Nucleosome Positioning in P. falciparum The authors should acknowledge that +1 nucleosomes have been previously reported in P. falciparum. For example, Kensche et al. (2016) used MNase-seq to map ~2,278 TSSs (based on enriched 5′-end RNA data) and found that the +1 nucleosome is positioned directly over the TSS in most genes:

"Analysis of 2278 start sites uncovered positioning of a +1 nucleosome right over the TSS in almost all analysed regions" (Figure 3A).

They also described a nucleosome-depleted region (NDR) upstream of the TSS, which varies in size, while the +1 nucleosome frequently overlaps the TSS. The authors should nuance their claims accordingly. Nevertheless, I do agree that the +1 positioning in P. falciparum may be fuzzier as compared to yeast or mammals. Moreover, the correlation between +1 nucleosome occupancy and gene expression is often weak and that several genes show similar nucleosome profiles regardless of expression level. This raises my question: did the authors observe any of these patterns in their new data?

We appreciate the reviewer’s insightful comment and agree that +1 nucleosomes and nucleosome depleted promoter regions have been previously reported in P. falciparum, notably by the Bartfai and Le Roch groups, including Kensche et al. (PMID: 26578577). Our study advances this understanding by providing, for the first time, a comprehensive view of the entirety of a canonical eukaryotic promoter architecture in P. falciparum—encompassing the NDR, the well-positioned +1 nucleosome, and the downstream phased nucleosome array. This downstream nucleosome array structure has not been characterized before, as prior studies noted a “lack of downstream nucleosomal arrays” (PMID: 26578577) or “relatively random” nucleosome organization within gene bodies (PMID: 24885191). We have revised the manuscript to more clearly acknowledge previous work and highlight our contributions. The changes we applied in the manuscript are highlighted in yellow and shown as well below.

In the Abstract L26-L230: Contrary to the current view of irregular chromatin, we demonstrate for the first time regular phased nucleosome arrays downstream of TSSs, which, together with the established +1 nucleosome and upstream nucleosome-depleted region, reveal a complete canonical eukaryotic promoter architecture in Pf.

Introduction L156-L159: For example, we identify a phased nucleosome array downstream of the TSS. Together with a well-positioned +1 nucleosome and an upstream nucleosome-free region. These findings support a promoter architecture in Pf that resembles classical eukaryotic promoters (Bunnik et al. 2014, Kensche et al. 2016).

Results L181-L183: These new Pf nucleosome maps reveal a nucleosome organisation at transcription start sites (TSS) reminiscent of the general eukaryotic chromatin structure, featuring a reported well-positioned +1 nucleosome , an upstream nucleosome-free region (NFR, Bunnik et al. 2014, Kensche et al. 2016), and shown for the first time in Pf, a phased nucleosome array downstream of the TSS.

Discussion L414-L419: Previous analyses of Pf chromatin have identified +1 nucleosomes and NFRs (Bunnik et al 2014, Kensche et al. 2016). Here we extend this understanding by demonstrating phased nucleosome array structures throughout the genome. This finding provides evidence for a spatial regulation of nucleosome positioning in Pf, challenging the notion that nucleosome positioning is relatively random in gene bodies (Bunnik et al. 2014, Kensche et al. 2016). Consequently our results contribute to the understanding that Pf exhibits a typical eukaryotic chromatin structure, including well-defined nucleosome positioning at the TSS and regularly spaced nucleosome arrays (Schones et al. 2008; Yuan et al. 2005).

Regarding the reviewer’s question on +1 nucleosome dynamics. Our data agrees with the reviewer and other studies (e.g. PMID: 31694866), that the +1 nucleosome position is robust and does not correlate with gene expression strength. In the manuscript we show that dynamic nucleosomes are preferentially detected at the –1 nucleosome position (Figure 2C). In line with that we show that the +1 nucleosome position does not markedly change during transcription initiation of a subset of late transcribed genes (Figure 5A). However, we observe an opening of the NDR and within the gene body increased fuzziness and decreased nucleosome array regularity (Figure S4A). To illustrate the relationship between the +1 nucleosome positioning and expression strength, we have included a heatmap showing nucleosome occupancy at the TSS, ordered according to expression strength (NEW Figure S4C):

We included a sentence describing the relationship of +1 nucleosome position with gene expression in L257-L258: Furthermore, the +1 nucleosome positioning is unaffected by the strength of gene expression (Figure S2C).

__ Lack of Quality Control in the Pipeline __

The authors claim (lines 152-153) that QC is performed at every stage, but this is not supported by the implementation. On the GitHub page (GitHub - uschwartz/nucDetective), QC steps are only marked at the Profiler stage using standard tools (FastQC, MultiQC). The Inspector stage, which is crucial for validating nucleosome detection, lacks QC entirely. The authors should implement additional steps to assess the quality of nucleosome calls. For example, how are false positives managed? ROC curves should be used to evaluate true positive vs. false positive rates when defining dynamic nucleosomes. How sequencing biases are adressed?

The workflow overview chart on GitHub was not properly color coded. Therefore, we changed the graphics and highlighted the QC steps in the overview charts accordingly:

Based on our long standing expertise of analysing MNase-seq data (PMID: 38959309, PMID: 37641864, PMID: 30496478, PMID: 25608606), the best quality metrics to assess the performance of the challenging MNase experiment are the fragment size distributions revealing the typical nucleosomal DNA lengths and the TSS plots showing a positioned +1 nucleosome and regularly phased nucleosome arrays downstream of the +1 nucleosome. Additionally, visual inspection of the nucleosome profiles in a genome browser is advisable. We make those quality metrics easily available in the nucDetective Profiler workflow (Insertsize Histogram, TSS plot and provide nucleosome profile bigwig files). Furthermore, the PC and correlation analysis based on the nucleosome occupancy in the inspector workflow allows to evaluate replicate reproducibility or integrity of time series data, as shown for data evaluated in this manuscript.

The inspector workflow uses the well-established DANPOS toolkit to call nucleosome positions. Based on our experience, this step is particularly robust and well-established in the DANPOS toolkit (PMID: 23193179), so there is no need to reinvent it. Nevertheless, appropriate pre-processing of the data as done in the nucDetective pipeline is crucial to obtain highly resolved nucleosome positions. Using the final nucleosome profiles (bigwig) and the nucleosome reference positions (bed) as output of the Inspector workflow allows visual inspection of the called nucleosomes in a genome viewer. Furthermore, to avoid using false positive nucleosome positions for dynamic nucleosome analysis, we take only the 20% best positioned nucleosomes of each sample, as determined by the fuzziness score.

We understand the value of a gold standard of dynamic nucleosomes to test performance using ROC curves. However, we are not aware that such a gold standard exists in the nucleosome analysis field, especially not when using multi-sample settings, such as time series data. One alternative would be to use simulated data; however, this has several limitations:

• __Lack of biological complexity: __simulated data often fails to capture the full complexity of biological systems including the heterogeneity, variability, and subtle dependencies present in real-world data. Simplifications and omissions in simulation models can result in test datasets that are more tractable but less realistic, causing software to appear robust or accurate under idealized conditions, while underperforming on actual experimental data.
• __Risks of Overfitting: __Software may be tuned to perform well on simulated datasets leading to overfitting and falsely inflated performance metrics. This undermines the predictive or diagnostic value of the results for real biological data

• Poor Model Fidelity and Hidden Assumptions: The authenticity of simulated data is bounded by the fidelity of the underlying models. If those models are inaccurate or make untested assumptions, the generated data may not reflect real experimental or clinical scenarios. This can mask software shortcomings or bias validation toward specific, perhaps irrelevant, scenarios. Therefore, we decided to validate the performance of the pipeline in the biological context of the analyzed data:

• PCA analysis of the individual nucleosome features shows a cyclic structure as expected for the IDC (Fig. 1D-G).

• Nucleosome occupancy changes anti-correlate with chromatin accessibility (Fig. 3B) as expected.
• Dynamic nucleosome features correlate with expression changes (Fig. 5C) We are aware that MNase-seq experiments might have sequence bias caused by the enzyme's endonuclease sequence preference (PMID: 30496478). However, the main aim of the nucDetective pipeline is to identify dynamic nucleosome features genome wide. Therefore, we are comparing the nucleosome features across multiple samples to find the positions in the genome with the highest variability. Comparisons are performed between the same nucleosome positions at the same genomic sites across multiple conditions, so the sequence context is constant and does not confound the analysis. This is like the differential expression analysis of RNA-seq data, where the gene counts are not normalized by gene length. Introducing a sequence normalization step might distort and bias the results of dynamic nucleosomes.

We included a paragraph describing the limitations to the discussion (L447-457):

Depending on the degree of MNase digestion, preferentially nucleosomes from GC rich regions are revealed in MNase-seq experiments (Schwartz et al. 2019). However, no sequence or gDNA normalisation step was included in the nucDetective pipeline. To identify dynamic nucleosomes, comparisons are performed between the same nucleosome positions at the same genomic sites across multiple samples. Hence, the sequence context is constant and does not confound the analysis. Introducing a sequence normalization step might even distort and bias the results. Nevertheless, it is highly advisable to use low MNase concentrations in chromatin digestions to reduce the sequence bias in nucleosome extractions. This turned out to be a crucial condition to obtain a homogenous nucleosome distribution in the AT-rich intergenic regions of eukaryotic genomes and especially in the AT-rich genome of Pf (Schwartz et al. 2019, Kensche et al. 2016).

__ Use of Mono-nucleosomes Only __

The authors re-analyze the Kensche et al. (2016) dataset using only mono-nucleosomes and claim improved nucleosome profiles, including identification of tandem arrays previously unreported in P. falciparum. Two key issues arise: 1. Is the apparent improvement due simply to focusing on mono-nucleosomes (as implied in lines 342-346)?

The default setting in nucDetective is to use fragment sizes of 140 – 200 bp, which corresponds to the main mono-nucleosome fraction in standard MNase-seq experiments. However, the correct selection of fragment sizes may vary depending on the organism and the variations in MNase-seq protocols. Therefore, the pipeline offers the option of changing the cutoff parameter (--minLen; --maxLen), accordingly. Kensche et al thoroughly tested and established the best parameters for the data set. We agree with their selected parameters and used the same cutoffs (75-175 bp) in this manuscript. For this particular data set, the fragment size selection is not the reason why we obtain a better resolution. MNase-seq analysis is a multistep process which is optimized in the nucDetective pipeline. Differences in the analysis to Kensche et al are at the pre-processing stage and alignment step:

Kensche et al. : “Paired-end reads were clipped to 72 bp and all data was mapped with BWA sample (Version 0.6.2-r126)”

nucDetective:

• Trimming using TrimGalore --paired -q 10 --stringency 2
• Mapping using bowtie2 --very-sensitive –dovetail --no-discordant
• MAPQ >= 20 filtering of aligned read-pairs (samtools). The manuscript text L379 was changed to

This is achieved using MNase-seq optimized alignment settings, and proper selection of the fragment sizes corresponding to mono-nucleosomal DNA to obtain high resolution nucleosome profiles.

How does the pipeline perform with di- or tri-nucleosomes, which are also biologically relevant (Kensche et al., 2016 and others)? Furthermore, the limitation to mono-nucleosomes is only mentioned in the methods, not in the results or discussion, which could mislead readers.

The pipeline is optimized for mono-nucleosome analysis. However, the cutoffs for fragment size selection can be adjusted to analyse other fragment populations in MNase-seq data (--minLen; --maxLen). For example we know from previous studies that the settings in the pipeline could be used for sub-nucleosome analysis as well (PMID: 38959309). Di- or Tri-nucleosome analysis we have not explicitly tested. However, in a previous study (PMID: 30496478) we observed that the inherited MNase sequence bias is more pronounced in di-nucleosomes, which are preferentially isolated from GC-rich regions. This is in line with the depletion of di-nucleosomes in AT-rich intergenic regions in Pf, as was already described by Kensche et al.

Changes to the manuscript text: We included a paragraph describing the limitations to the discussion (L428-434):

The nucDetective pipeline has been optimized for the analysis of mono-nucleosomes. However, the selection of fragment sizes can be adjusted manually, enabling the pipeline to be used for other nucleosome categories. The pipeline is suitable to map and annotate sub-nucleosomal particles (

__ Reference Nucleosome Numbers __

The authors identify 49,999 reference nucleosome positions. How does this compare to previous analyses of similar datasets? This should be explicitly addressed.

We thank the reviewer for this suggestion. In order to put our results in perspective, it is important to distinguish between reference nucleosome positions (what we reported in the manuscript) and all detectable nucleosomes. The reference positions are our attempt to build a set of nucleosome positions with strong evidence, allowing confident further analysis across timepoints. The selection of a well positioned subset of nucleosomes for downstream analysis has been done previously (PMID: 26578577) and the merging algorithm we used across timepoints is also used by DANPOS to decide if a MNase-Seq peak is a new nucleosome position or belongs to an existing position (PMID: 23193179).

To be able to address the reviewer suggestion we prepared and added a table to the supplementary data, including the total number of all nucleosomes detected by our pipeline at each timepoint. We adjusted the results to the following (L223-226):

“The pipeline identified a total of 127370 ± 1151 (mean ± SD) nucleosomes at each timepoint (Supplementary Data X). To exclude false positive positions in our analysis, we conservatively selected 49,999 reference nucleosome positions, representing sites with a well-positioned nucleosome at least at one time point (see Methods). Among these 1192 nucleosomes exhibited […]”

Several groups reported nucleosome positioning data for P. falciparum (PMID: 20015349, PMID: 20054063, PMID: 24885191, PMID: 26578577), however only Ponts et al (2010) reported resolved numbers (~45000-90000 nucleosomes depending in development stage) and Bunnik et al reported ~ 75000 nucleosomes in a graph. Although we do not know the reason of why the other studies did not include specific numbers, we speculate that the data quality did not allow them to confidently report a number. In fact, nucleosomal reads are severely depleted in AT-rich intergenic regions in the Ponts and Bunnik datasets. In contrast, Kensche et al (and our analysis) shows that nucleosomes can be identified throughout the genome of Pf. Therefore, the nucleosome numbers reported by Ponts et al and Bunnik et al are very likely underestimated.

We included the following text in the discussion, addressing previously published datasets (L404 – 405):

“For example, our pipeline was able to identify a total of ~127,000 nucleosomes per timepoint (=5.4 per kb) in range with observed nucleosome densities in other eukaryotes (typically 5 to 6 per kb). From these, we extracted 49,999 reference nucleosome positions with strong positioning evidence across all timepoints, which we used to characterize nucleosome dynamics of Pf longitudinally. Previous studies of P. falciparum chromatin organization, did not report a total number of nucleosomes (Westenberger et al. 2009, Kensche et al. 2016), or estimated approximately ~45000-90000 nucleosomes across the genome at different developmental stages (Bunnik et al. 2014, Ponts et al. 2010). However, this value likely represents an underestimation due to the depletion of nucleosomal reads in AT-rich intergenic regions observed in their datasets.”

__ Figure 1B and Nucleosome Spacing __

The authors claim that Figure 1B shows developmental stage-specific variation in nucleosome spacing. However, only T35 shows a visible upstream change at position 0. In A4, A6, and A8 (Figure S4), no major change is apparent. Statistical tests are needed to validate whether the observed differences are significant and should be described in the figure legends and main text.

We would like to thank the reviewer for bringing this issue to our attention. We apologize for an error we made, wrongly labelling the figure numbers. The differences in nucleosome spacing across time are visible in Figure 1C. Figure 1B shows the precise array structure of the Pf nucleosomes, when centered on the +1 nucleosome, and is mentioned before. The mistake is now corrected.

In Figure 1C the mean NRL and 95% confidence interval are depicted, allowing a visual assessment of data significance (non-overlapping 95% CI-Intervals correspond to p Taken together we corrected this mistake and edited the text as follows (L194 – 199):

“With this +1 nucleosome annotation, regularly spaced nucleosome arrays downstream of the TSS were detected, revealing a precise nucleosome organization in Pf (Figure 1B). Due to the high resolution maps of nucleosomes we can now observe significantvariations in nucleosome spacing depending on the developmental stage (Figure 1C, ANOVA on bootstrapped values (3 per timepoint) F₇,₇₂ = 35.10, p

__ Genome-wide Occupancy Claims __

The claim that nucleosomes are "evenly distributed throughout the genome" (Figure S2A) is questionable. Chromosomes 3 and 11 show strong peaks mid-chromosome, and chromosome 14 shows little to no signal at the ends. This should be discussed. Subtelomeric regions, such as those containing var genes, are known to have unique chromatin features. For instance, Lopez-Rubio et al. (2009) show that subtelomeric regions are enriched for H3K9me3 and HP1, correlating with gene silencing. Should these regions not display different nucleosome distributions? Do you expect the Plasmodium genome (or any genome) to have uniform nucleosome distribution?

On global scale (> 10 kb) we would expect a homogenous distribution of nucleosomes genome wide, regardless of euchromatin or heterochromatin. We have shown this in a previous study for human cells (PMID: 30496478), which was later confirmed for drosophila melongaster (PMID: 31519205,PMID: 30496478) and yeast (PMID: 39587299).

However, Figure S2A shows the distribution of the dynamic nucleosome features during the IDC, called with our pipeline. We agree with the reviewer, that there are a few exceptions of the uniform distribution, which we address now in the manuscript.

Furthermore, we agree with the reviewer that the H3K9me3 / HP1 subtelomeric regions are special. Those regions are depleted of dynamic nucleosomes in the IDC as shown in Fig. 2D and now mentioned in L280 - L282.

We included an additional genome browser snapshot in Supplemental Figure S2B and changed the text accordingly (L245-249):

We observed a few exceptions to the even distribution of the nucleosomes in the center of chromosome 3, 11 and 12, where nucleosome occupancy changes accumulated at centromeric regions (Figure S2B). Furthermore, the ends of the chromosomes are rather depleted of dynamic nucleosome features.

Genome browser snapshot illustrating accumulation of nucleosome occupancy changes at a centromeric site. Centered nucleosome coverage tracks (T5-T40 colored coverage tracks), nucleosomes occupancy changes (yellow bar) and annotated centromers (grey bar) taken from (Hoeijmakers et al., 2012)

Dependence on DANPOS

The authors criticize the DANPOS pipeline for its limitations but use it extensively within nucDetective. This contradiction confuses the reader. Is nucDetective an original pipeline, or a wrapper built on existing tools?

One unique feature of the nucDetective pipeline is to identify dynamic nucleosomes (occupancy, fuzziness, regularity, shifts) in complex experimental designs, such as time series data (Inspector workflow). To our knowledge, there is no other tool for MNase-seq data which allows multi-condition/time-series comparisons (PMID: 35061087). For example, DANPOS allows only pair-wise comparisons, which cannot be used for time-series data. For the analysis of dynamic nucleosome features we require nucleosome profiles and positions at high resolution. For this purpose, several tools do already exist (PMID: 35061087). However, researchers without experience in MNase-seq analysis often find the plethora of available tools overwhelming, which makes it challenging to select the most appropriate ones. Here we share our experience and provide the user an automated workflow (Profiler), which builds on existing tools.

In summary the Profiler workflow is a wrapper built on existing tools and the Inspector workflow is partly a wrapper (uses DANPOS to normalize nucleosome profiles and call nucleosome positions) and implements our original algorithm to detect dynamic nucleosome features in multiple conditions / time-series data.

__ Control Data Usage __

The authors should clarify whether gDNA controls were used throughout the analysis, as done in Kensche et al. (2016). Currently, this is mentioned only in the figure legend for Figure 5, not in the methods or results.

We used the gDNA normalisation to optimize the visualization of the nucleosome depleted region upstream of the TSS in Fig 5A. Otherwise, we did not normalize the data by the gDNA control. The reason is the same as we did not include sequence normalization in the pipeline (see comment above)

We included a paragraph describing the limitations to the discussion (L447-457):

Depending on the degree of MNase digestion, preferentially nucleosomes from GC rich regions are revealed in MNase-seq experiments (Schwartz et al. 2019). However, no sequence or gDNA normalisation step was included in the nucDetective pipeline. To identify dynamic nucleosomes, comparisons are performed between the same nucleosome positions at the same genomic sites across multiple samples. Hence, the sequence context is constant and does not confound the analysis. Introducing a sequence normalization step might even distort and bias the results. Nevertheless, it is highly advisable to use low MNase concentrations in chromatin digestions to reduce the sequence bias in nucleosome extractions. This turned out to be a crucial condition to obtain a homogenous nucleosome distribution in the AT-rich intergenic regions of eukaryotic genomes and especially in the AT-rich genome of Pf (Schwartz et al. 2019, Kensche et al. 2016).

We added following statement to the methods part: Additionally, the TSS profile shown in Figure 5A was normalized by the gDNA control for better NDR visualization.

__ Lack of Statistical Power for Time-Series Analyses __

Although the pipeline is presented as suitable for time-series data, it lacks statistical tools to determine whether differences in nucleosome positioning or fuzziness are significant across conditions. Visual interpretation alone is insufficient. Statistical support is essential for any differential analysis.

We understand the value of statistical support in such an analysis. However, in biology we often face the limitations in terms of the appropriate sample sizes needed to accurately estimate the variance parameters required for statistical modeling. As MNase-seq experiments require a large amount of input material and high sequencing depth, the number of samples in most experiments is low, often with only two replicates (PMID: 23193179). Therefore, we decided that the nucDetective pipeline should be rather handled as a screening method to identify nucleosome features with high variance across all conditions. This prevents misuse of p-values. A common misinterpretation we observed is the use of non-significant p-values to conclude that no biological change exists, despite inadequate statistical power to detect such changes. We included a paragraph in the limitations section discussing the limitations of statistical analysis of MNase-Seq data.

Changes to the manuscript text: We included a paragraph describing the limitations to the discussion (L435-446).

As MNase-seq experiments require a large amount of input material and high sequencing depths, most published MNase-seq experiments do not provide the appropriate sample sizes required to accurately estimate the variance parameters necessary for statistical modelling (Chen et al. 2013). Therefore, dynamic nucleosomes are not identified through statistical testing but rather by ranking nucleosome features according to their variance across all samples and applying a variance threshold to distinguish them. This concept is well established to identify super-enhancers (Whyte et al. 2013). In this study we set the variance cutoff to a slope of 3, resulting in a high data confidence. However, other data sets might require further adjustment of the variance cutoff, depending on data quality or sequencing depth. The nucDetective identification of dynamic nucleosomes can be seen as a screening approach to provide a holistic overview of nucleosome dynamics in the system, which provides a basis for further research.

Reproducibility of Methods

The Methods section is not sufficient to reproduce the results. The GitHub repository lacks the necessary code to generate the paper's figures and focuses on an exemplary yeast dataset. The authors should either: o Update the repository with relevant scripts and examples, o Clearly state the repository's purpose, or o Remove the link entirely. Readers must understand that nucDetective is dedicated to assessing nucleosome fuzziness, occupancy, shift, and regularity dynamics-not downstream analyses presented in the paper.

We thank the reviewer for this helpful comment. In addition to the main nucDetective repository, a second GitHub link is provided in the Data Availability section, which contains the scripts used to generate the figures presented in the paper. This separation was intentional to distinguish the general-purpose nucDetective tool from the project-specific analyses performed for this study. We acknowledge that this may not have been sufficiently clear.

To have all resources available at a single citable permanent location we included a link to the corresponding Zenodo repository (https://doi.org/10.5281/zenodo.16779899) in the Data and materials availability statement.

The Zenodo repository contains:

Code (scripts.zip) and annotation of Plasmodium falciparum (Annotation.zip) to reproduce the nucDetective v1.1 (nucDetective-1.1.zip) analysis as done in the research manuscript entitled "Deciphering chromatin architecture and dynamics in Plasmodium falciparum using the nucDetective pipeline".

The folder "output_nucDetective" conains the complete output of the nucDetective analysis pipeline as generated by the "01_nucDetective_profiler.sh" and "02_nucDetective_inspector.sh" scripts.

Nucleosome coverage tracks, annotation of nucleosome positions and dynamic nucleosomes are deposited additonally in the folder "Pf_nucleosome_annotation_of_nucDetective".

To make this clearer we added following text to Material and Methods in ”The nucDetective pipeline” section:

Changes in the manuscript text (L518-519):

The code, software and annotations used to run the nucDetective pipeline along with the output have been deposited on Zenodo (https://doi.org/10.5281/zenodo.16779899).

__ Supplementary Tables __

Including supplementary tables showing pipeline outputs (e.g., nucleosome scores, heatmaps, TSS extraction) would help readers understand the input-output structure and support figure interpretations.

See comments above.

We included a link to the corresponding Zenodo repository (https://doi.org/10.5281/zenodo.16779899) in the Data and materials availability statement.

The repository contains:

Code (scripts.zip) and annotation of Plasmodium falciparum (Annotation.zip) to reproduce the nucDetective v1.1 (nucDetective-1.1.zip) analysis as done in the research manuscript entitled "Deciphering chromatin architecture and dynamics in Plasmodium falciparum using the nucDetective pipeline".

The folder "output_nucDetective" conains the complete output of the nucDetective analysis pipeline as generated by the "01_nucDetective_profiler.sh" and "02_nucDetective_inspector.sh" scripts.

Minor Comments:

The authors should moderate claims such as "no studies have reported a well-positioned +1 nucleosome" in P. falciparum, as this contradicts existing literature. Similarly, avoid statements like "poorly understood chromatin architecture of Pf," which undervalue extensive prior work (e.g., discovery of histone lactylation in Plasmodium, Merrick et al., 2023).

We would like to clarify that we neither wrote that ““no studies have reported a well-positioned +1 nucleosome”” in P. falciparum nor did we intend to imply such thing. However, we acknowledge that our original wording may have been unclear. To address this, we have revised the manuscript to explicitly acknowledge prior studies on chromatin organization and highlight our contribution.

In the Abstract L26-L30: Contrary to the current view of irregular chromatin, we demonstrate for the first time regular phased nucleosome arrays downstream of TSSs, which, together with the established +1 nucleosome and upstream nucleosome-depleted region, reveal a complete canonical eukaryotic promoter architecture in Pf.

Introduction L156-L159: For example, we identify a phased nucleosome array downstream of the TSS. Together with a well-positioned +1 nucleosome and an upstream nucleosome-free region. These findings support a promoter architecture in Pf that resembles classical eukaryotic promoters (Bunnik et al. 2014, Kensche et al. 2016).

Results L180-L183: These new Pf nucleosome maps reveal a nucleosome organisation at transcription start sites (TSS) reminiscent of the general eukaryotic chromatin structure, featuring a reported well-positioned +1 nucleosome , an upstream nucleosome-free region (NFR, Bunnik et al. 2014, Kensche et al. 2016), and shown for the first time in Pf, a phased nucleosome array downstream of the TSS.

Discussion L412-L421: Previous analyses of Pf chromatin have identified +1 nucleosomes and NFRs (Bunnik et al 2014, Kensche et al. 2016). Here we extend this understanding by demonstrating phased nucleosome array structures throughout the genome. This finding provides evidence for a spatial regulation of nucleosome positioning in Pf, challenging the notion that nucleosome positioning is relatively random in gene bodies (Bunnik et al. 2014, Kensche et al. 2016). Consequently our results contribute to the understanding that Pf exhibits a typical eukaryotic chromatin structure, including well-defined nucleosome positioning at the TSS and regularly spaced nucleosome arrays (Schones et al. 2008; Yuan et al. 2005).

The phrase “poorly understood chromatin architecture” has been modified to “underexplored chromatin architecture” in order to more accurately reflect the potential for further analyses and contributions to the field, while avoiding any potential misinterpretation of an attempt to undervalue previous work.

Track labels in figures (e.g., Figure 5B) are too small to be legible.

We made the labels bigger.

Several figures (e.g., Figure 5B, S4B) lack statistical significance tests. Are the differences marked with stars statistically significant or just visually different?

We added statistics to S4B.

Differences in 5B were identified by visual inspection. To clarify this, we exchanged the asterisks to arrows in Fig.5B and changed the text in the legend:

Arrows mark descriptive visual differences in nucleosome occupancy.

Figure S3 includes a small black line on top of the table. Is this an accidental crop?

We checked the figure carefully; however, the black line does not appear in our PDF viewer or on the printed paper

The authors should state the weaknesses and limitations of this pipeline.

We added a limitation section in discussion, see comments above

Reviewer #1 (Significance (Required)):

The proposed pipeline is useful and timely. It can benefit research groups willing to analyse MNase-Seq data of complex genomes such as P. falciparum. The tool requires users to have extensive experience in coding as the authors didn't include any clear and explicit codes on how to start processing the data from raw files. Nevertheless, there are multiple tool that can detect nucleosome occupancy and that are not cited by the authors not mention. I have included for the authors a link where a large list of tools for analysis of nucleosome positioning experiments tools/pipelines were developed for (Software to analyse nucleosome positioning experiments - Gene Regulation - Teif Lab). I think it would be useful for the authors to direct the reference this.

We appreciate the reviewer’s valuable suggestion. We included a citation to the comprehensive database of nucleosome analysis tools curated by the Teif lab (Shtumpf et al., 2022). We chose to reference only selected tools in addition to this resource rather than listing all individual tools to maintain clarity and avoid overloading the manuscript with numerous citations.

Despite valid, I still believe that controlling their pipeline by filtering out false positives and including more QC steps at the Inspector stage is strongly needed. That would boost the significance of this pipeline.

We thank the reviewer for the assessment of our study and for recognizing that our MNase-seq analysis pipeline nucDetective can be a useful tool for the chromatin community utilizing MNase-Seq in complex settings.

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

In this manuscript, Holzinger and colleagues have developed a new pipeline to assess chromatin organization in linear space and time. They used this pipeline to reevaluate nucleosome organization in the malaria parasite, P. falciparum. Their analysis revealed typical arrangement of nucleosomes around the transcriptional start site. Furthermore, it further strengthened and refined the connection between specific nucleosome dynamics and epigenetic marks, transcription factor binding sites or transcriptional activity.

Major comments

• I am wondering what is the main selling point of this manuscript is. If it is the development of the nucDetective pipeline, perhaps it would be best to first benchmark it and directly compare it to existing tools on a dataset where nucleosome fussiness, shifting and regularity has been analyzed before. If on the other hand, new insights into Plasmodium chromatin biology is the primary target validation of some of the novel findings would be advantageous (e.g. refinement of TSS positions, relevance of novel motifs, etc).

NucDetective presents a novel pipeline to identify dynamic nucleosome properties within different datasets, like time series or developmental stages, as analysed for the erythrocytic cycle in this manuscript. As such kind of a pipeline, allowing direct comparisons, does not exist for MNase-Seq data, we used the existing analysis and high quality dataset of Kensche et al., to visualize the strong improvements of this kind of analysis. Accordingly, we combined the pipeline development and the reasearch of chromatin structure analysis, being able to showcase the utility of this new pipeline.

• The authors identify a strong positioning of +1 nucleosome by searching for a positioned nucleosomes in the vicinity of the assigned TSS. Given the ill-defined nature of TSSs, this approach sounds logic at first glance. However, given the rather broad search space from -100 till +300bp, I am wondering whether it is a sort of "self-fulfilling prophecy". Conversely, it would be good to validate that this approach indeed helps to refine TSS positions.

We thank the reviewer for raising this important point. We would like to clarify that we do not claim to redefine or precisely determine TSS positions in our study. Instead, we use annotated TSS coordinates as a reference to identify nucleosomes that correspond to the +1 nucleosome, based on their proximity to the TSS.

We selected the search window from -100 to +300 bp to account for known variability in Pf TSS annotation. For example, dominant transcription start sites identified by 5'UTR-seq tag clusters can differ by several hundred base pairs within a single time point (Chappell et al., 2020). The broad window thus allows us to capture the principal nucleosome positions near a TSS, even when the TSS itself is imprecise or heterogeneous. Based on the TSS centered plots (Figure 2C and Figure S1B), we reasoned that a window of -100 to +300 is sufficient to capture the majority of the +1 nucleosomes, which would have been missed by using smaller window sizes. This strategy aligns with well-established conventions in yeast chromatin biology, where the +1 nucleosome is defined relative to the TSS (Jiang and Pugh, 2009; Zhang et al. 2011) and commonly used as an anchor point to visualize downstream phased nucleosome arrays and upstream nucleosome-depleted regions (Rossi et al., 2021; Oberbeckmann et al., 2019; Krietenstein et al., 2016 and many more). Accordingly, our approach leverages these accepted standards to interpret nucleosome positioning without re-defining TSS annotations.

• Figure 1C: I am wondering how should the reader interpret the changes in nucleosomal repeat length changes throughout the cycle. Is linker DNA on average 10 nucleotides shorter at T30 compared to T5 timepoint? If so how could such "dramatic reorganization" be achieved at the molecular level in absence of a known linker DNA-binding protein. More importantly is this observation supported by additional evidence (e.g. dinucleosomal fragment length) or could it be due to slightly different digestion of the chromatin at the different stages or other technical variables?

We thank the reviewer for this insightful question regarding the interpretation of NRL changes across the cell cycle. The reviewer is right in her or his interpretation – linker DNA is on average ~10 bp shorter at T30 than at T5.

To address concerns about additional evidence and potential MNase digestion variability, we now analyzed MNase-seq fragment sizes by shifting mononucleosome peaks of each time point to the canonical 147 bp length, to correct for MNase digestion differences. After this normalisation, dinucleosome fragment length distributions revealed the shortest linker lengths at T30 and T35, whereas T5 and T10 showed longer DNA linkers. These results confirm our previous NRL measurements based on mononucleosomal read distances while controlling for MNase digestion bias.

The molecular basis of this reorganization, is still unclear. While linker histone H1 is considered absent in Plasmodium falciparum, presence of an uncharacterized linker DNA–binding protein or alternative factors fulfilling a similar role can not be excluded (Gill et al. 2010). However, H1 absence across all developmental stages, fails to explain stage-specific chromatin changes. We hypothesize that Apicomplexans evolved specialized chromatin remodelers to compensate for the missing H1, which may also drive the dynamic NRL changes observed. The low NRL coincides with high transcriptional activity in Pf during trophozoite stage is consistent with previous reports linking elevated transcription to reduced NRL in other eukaryotes (Baldi et al. 2018). In addition, the schizont stage involves multiple rounds of DNA replication requiring large histone supplies being produced during that time. It may well be that a high level of histone synthesis and DNA amplification, results in a short time period with increased nucleosome density and shorter NRL, until the system reaches again equilibrium (Beshnova et al. 2014). Although speculative we suggest a model wherein increased transcription promotes elevated nucleosome turnover and re-assembly by specialized remodeling enzymes, combined with high abundance of histones, resulting in higher nucleosome density and decreased NRL. Unfortunately, absolute quantification of nucleosome levels from this MNase-seq dataset is not possible without spike-in controls, which makes it infeasible to test the hypothesis with the available data set (Chen et al. 2016).

Minor comments

• I am wondering whether fuzziness and occupancy changes are truly independent categories. I am asking as both could lead to reduction of the signal at the nucleosome dyad and because they show markedly similar distribution in relation to the TSS and associate with identical epigenetic features (Figure 2B-D). Figure 2A indicates minimal overlap between them, but this could be due to the fact that the criteria to define these subtypes is defined such to place nucleosomes to one or the other category, but at the end they represent two flavors of the same thing.

Indeed, changes in occupancy and fuzziness can appear related because both features may reduce signal intensity at the nucleosome dyad and both are connected to “poor nucleosome positioning”. However, their definitions and measurements are clearly distinct and technically independent. Occupancy reflects the peak height at the nucleosome dyad, while fuzziness quantifies the spread of reads around the peak, measured as the standard deviation of read positions within each nucleosome peak (Jiang and Pugh, 2009; Chen et al., 2013). Although a reduction in occupancy can contribute to increased fuzziness by diminishing the dyad axis signal, fuzziness primarily arises from increased variability in the flanking regions around the nucleosome position center. While this distinction is established in the field, it is also often confused by the concept of well (high occupancy, low fuzziness) and poorly (high fuzziness, low occupancy) positioned nucleosomes, where both of these features are considered.

• Do the authors detect spatial relationship between fuzzy and repositioned/evicted nucleosomes at the level of individual nucleosomes pairs. With other words, can fuzziness be the consequence of repositioning/eviction of the neighboring nucleosome?

In Figure 2A we analyse the spatial overlap of all features to each other. The analysis clearly shows that fuzziness, occupancy changes and position changes occur mostly at distinct spatial sites (overlaps between 3 and 10%, Fig. 2A). Therefore, we suggest that the features correspond to independent processes. Likewise, we do observe an overlap between occupancy and ATAC-seq peaks, but not nucleosome positioning shifts, clearly discriminating different processes.

• Figure 4: enrichment values and measure of statistical significance for the different motifs are missing. Also have there been any other motifs identified.

This information is present in Supplemental Figure S3. Here we show the top 3 hits in each cluster. In the figure legend of Figure 4 we reference to Fig. S3:

L1054 –1055:

“Additional enriched motifs along with the significance of motif enrichment and the fraction of motifs at the respective nucleosome positions are shown in Figure S3”

• The M&M would benefit from some more details, e.g. settings in the piepline, or which fragment sizes were used to map the MNase-seq data?

We included a link to the corresponding Zenodo repository (https://doi.org/10.5281/zenodo.16779899) in the Data and materials availability statement.

The repository contains:

Code (scripts.zip) and annotation of Plasmodium falciparum (Annotation.zip) to reproduce the nucDetective v1.1 (nucDetective-1.1.zip) analysis as done in the research manuscript entitled "Deciphering chromatin architecture and dynamics in Plasmodium falciparum using the nucDetective pipeline".

The folder "output_nucDetective" conains the complete output of the nucDetective analysis pipeline as generated by the "01_nucDetective_profiler.sh" and "02_nucDetective_inspector.sh" scripts.

Nucleosome coverage tracks, annotation of nucleosome positions and dynamic nucleosomes are deposited additonally in the folder "Pf_nucleosome_annotation_of_nucDetective".

To make this clearer we added following text to Material and Methods in ”The nucDetective pipeline” section:

Changes in the manuscript (L518-519):

The code, software and annotations used to run the nucDetective pipeline along with the output have been deposited on Zenodo (https://doi.org/10.5281/zenodo.16779899).

which fragment sizes were used to map the MNase-seq data?

The default setting in nucDetective is to use fragment sizes of 140 – 200 bp, which corresponds to the main mono-nucleosome fraction in standard MNase-seq experiments. However, the correct selection of fragment sizes may vary depending on the organism and the variations in MNase-seq protocols. Therefore, the pipeline offers the option of changing the cutoff parameter (--minLen; --maxLen), accordingly. Kensche et al thoroughly tested the best selection of the fragment sizes for the data set, which is used in this manuscript. We agree with their selection and used the same cutoffs (75-175 bp).

This is stated in line 535-536:

The fragments are further filtered to mono-nucleosome sized fragments (here we used 75 – 175 bp)

We changed the text:

The fragments are further filtered to mono-nucleosome sized fragments (default setting 140-200 bp; changed in this study to 75 – 175 bp)

We highlighted other parameters used in this study in the material and methods part.

Reviewer #2 (Significance (Required)):

Overall, the manuscript is well written and findings are clearly and elegantly presented. The manuscript describes a new pipeline to map and analyze MNase-seq data across different stages or conditions, though the broader applicability of the pipeline and advancements over existing tools could be better demonstrated. Importantly, the manuscript make use of this pipeline to provide a refined and likely more accurate view on (the dynamics of) nucleosome positioning over the AT-rich genome of P. falciparum. While these observations make sense they remain rather descriptive/associative and lack further experimental validation. Overall, this manuscript could be interest to both researchers working on chromatin biology and Plasmodium gene-regulation.

We thank the reviewer for the assessment of our study and for recognizing that the results of our MNase-seq analysis pipeline nucDetective contribute to a better understanding of Pf chromatin biology.

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

The manuscript "Deciphering chromatin architecture and dynamics in Plasmodium 2 falciparum using the nucDetective pipeline" describes computational analysis of previously published data of P falciparum chromatin. This work corrects the prevailing view that this parasitic organism has an unusually disorganized chromatin organization, which had been attributed to its high genomic AT content, lack of histone H1, and ancient derivation. The authors show that instead P falciparum has a very typical chromatin organization. Part of the refinement is due to aligning data on +1 nucleosome positions instead of TSSs, which have been poorly mapped. The computational tools corral some useful features, for querying epigenomic structure that make visualization straightforward, especially for fuzzy nucleosomes.

Reviewer #3 (Significance (Required)):

As a computational package this is a nice presentation of fairly central questions. The assessment and display of fuzzy nucleosomes is a nice feature.

We thank the reviewer for the assessment of our study and are pleased that the reviewer acknowledges the value and usability of our pipeline.

Reviewer #2 (Public review):

Summary:

This paper considers the effects of cognitive load (using an n-back task related to font color), predictability, and age on reading times in two experiments. There were main effects of all predictors, but more interesting effects of load and age on predictability. The effect of load is very interesting, but the manipulation of age is problematic, because we don't know what is predictable for different participants (in relation to their age). There are some theoretical concerns about prediction and predictability, and a need to address literature (reading time, visual world, ERP studies).

There is a major concern about the effects of age. See the results (155-190): this depends what is meant by word predictability. It's correct if it means the predictability in the corpus. But it may or may not be correct if it refers to how predictable a word is to an individual participant. The texts are unlikely to be equally predictable to different participants, and in particular to younger vs. older participants, because of their different experience. To put it informally, the newspaper articles may be more geared to the expectations of younger people. But there is also another problem: the LLM may have learned on the basis of language that has largely been produced by young people and so its predictions are based on what young people are likely to say. Both of these possibilities strike me as extremely likely. So it may be that older adults are affected more by words that they find surprising, but it is also possible that the texts are not what they expect, or the LLM predictions from the text are not the ones that they would make. In sum, I am not convinced that the authors can say anything about the effects of age unless they can determine what is predictable for different ages of participants. I suspect that this failure to control is an endemic problem in the literature on aging and language processing and needs to be systematically addressed.

Overall, I think the paper makes enough of a contribution with respect to load to be useful to the literature. But for discussion of age, we would need something like evidence of how younger and older adults would complete these texts (on a word-by-word basis) and that they were equally predictable for different ages. I assume there are ways to get LLMs to emulate different participant groups, but I doubt if we could be confident about their accuracy without a lot of testing. But without something like this, I think making claims about age would be quite misleading.

The authors respond to my summary comment by saying that prediction is individual and that they account for age-related effects in their models. But these aren't my concerns. Rather:

(1) The texts (these edited newspaper articles) could be more predictable for younger than older adults. If so, effects with older adults could simply be because people are less likely to predict less than more predictable words.

(2) The GPT-2 generated surprisal scores may correspond more closely to younger than older adult responses -- that is, its next word predictions may be more younger- than older-adult-like.

In my view, the authors have two choices: they could remove the discussion of age-related effects, or they could try to address BOTH (1) and (2).

As an aside, consider what we would conclude if we drew similar conclusions from a study in which children and adults read the same (children's) texts, but we didn't test what was predictable to each of them separately.

The paper is really strong in other respects and if my concern is not addressed, the conclusions about age might be generally accepted.

Author response:

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

Reviewer #1 (Public review):

This manuscript reports a dual-task experiment intended to test whether language prediction relies on executive resources, using surprisal-based measures of predictability and an n-back task to manipulate cognitive load. While the study addresses a question under debate, the current design and modeling framework fall short of supporting the central claims. Key components of cognitive load, such as task switching, word prediction vs integration, are not adequately modeled. Moreover, the weak consistency in replication undermines the robustness of the reported findings. Below unpacks each point. 

Cognitive load is a broad term. In the present study, it can be at least decomposed into the following components: 

(1)  Working memory (WM) load: news, color, and rank. 

(2)  Task switching load: domain of attention (color vs semantics), sensorimotor rules (c/m vs space).

(3)  Word comprehension load (hypothesized against): prediction, integration. 

The components of task switching load should be directly included in the statistical models. Switching of sensorimotor rules may be captured by the "n-back reaction" (binary) predictor. However, the switching of attended domains and the interaction between domain switching and rule complexity (1-back or 2-back) were not included. The attention control experiment (1) avoided useful statistical variation from the Read Only task, and (2) did not address interactions. More fundamentally, task-switching components should be directly modeled in both performance and full RT models to minimize selection bias. This principle also applies to other confounding factors, such as education level. While missing these important predictors, the current models have an abundance of predictors that are not so well motivated (see later comments). In sum, with the current models, one cannot determine whether the reduced performance or prolonged RT was due to affecting word prediction load (if it exists) or merely affecting the task switching load. 

The entropy and surprisal need to be more clearly interpreted and modeled in the context of the word comprehension process. The entropy concerns the "prediction" part of the word comprehension (before seeing the next word), whereas surprisal concerns the "integration" part as a posterior. This interpretation is similar to the authors writing in the Introduction that "Graded language predictions necessitate the active generation of hypotheses on upcoming words as well as the integration of prediction errors to inform future predictions [1,5]." However, the Results of this study largely ignored entropy (treating it as a fixed effect) and only focus on surprisal without clear justification. 

In Table S3, with original and replicated model fitting results, the only consistent interaction is surprisal x age x cognitive load [2-back vs. Reading Only]. None of the two-way interactions can be replicated. This is puzzling and undermines the robustness of the main claims of this paper. 

Reviewer #2 (Public review):

Summary

This paper considers the effects of cognitive load (using an n-back task related to font color), predictability, and age on reading times in two experiments. There were main effects of all predictors, but more interesting effects of load and age on predictability. The effect of load is very interesting, but the manipulation of age is problematic, because we don't know what is predictable for different participants (in relation to their age). There are some theoretical concerns about prediction and predictability, and a need to address literature (reading time, visual world, ERP studies). 

Strengths/weaknesses 

It is important to be clear that predictability is not the same as prediction. A predictable word is processed faster than an unpredictable word (something that has been known since the 1970/80s), e.g., Rayner, Schwanenfluegel, etc. But this could be due to ease of integration. I think this issue can probably be dealt with by careful writing (see point on line 18 below). To be clear, I do not believe that the effects reported here are due to integration alone (i.e., that nothing happens before the target word), but the evidence for this claim must come from actual demonstrations of prediction. 

The effect of load on the effects of predictability is very interesting (and also, I note that the fairly novel way of assessing load is itself valuable). Assuming that the experiments do measure prediction, it suggests that they are not cost-free, as is sometimes assumed. I think the researchers need to look closely at the visual world literature, most particularly the work of Huettig. (There is an isolated reference to Ito et al., but this is one of a large and highly relevant set of papers.) 

There is a major concern about the effects of age. See the Results (161-5): this depends on what is meant by word predictability. It's correct if it means the predictability in the corpus. But it may or may not be correct if it refers to how predictable a word is to an individual participant. The texts are unlikely to be equally predictable to different participants, and in particular to younger vs. older participants, because of their different experiences. To put it informally, the newspaper articles may be more geared to the expectations of younger people. But there is also another problem: the LLM may have learned on the basis of language that has largely been produced by young people, and so its predictions are based on what young people are likely to say. Both of these possibilities strike me as extremely likely. So it may be that older adults are affected more by words that they find surprising, but it is also possible that the texts are not what they expect, or the LLM predictions from the text are not the ones that they would make. In sum, I am not convinced that the authors can say anything about the effects of age unless they can determine what is predictable for different ages of participants. I suspect that this failure to control is an endemic problem in the literature on aging and language processing and needs to be systematically addressed. 

Overall, I think the paper makes enough of a contribution with respect to load to be useful to the literature. But for discussion of age, we would need something like evidence of how younger and older adults would complete these texts (on a word-by-word basis) and that they were equally predictable for different ages. I assume there are ways to get LLMs to emulate different participant groups, but I doubt that we could be confident about their accuracy without a lot of testing. But without something like this, I think making claims about age would be quite misleading. 

We thank both reviewers for their constructive feedback and for highlighting areas where our theoretical framing and analyses could be clarified and strengthened. We have carefully considered each of the points raised and made substantial additions and revisions.

As a summary, we have directly addressed the concerns raised by the reviewers by incorporating task-switching predictors into the statistical models, paralleling our focus on surprisal with a full analysis and interpretation of entropy, clarifying the robustness (and limitations) of the replicated findings, and addressing potential limitations in our Discussion.

We believe these revisions substantially strengthen the manuscript and improve the reading flow, while also clarifying the scope of our conclusions. We will not illustrate these changes in more detail:

(1) Cognitive load and task-switching components.

We agree that cognitive load is a multifaceted construct, particularly since our secondary task broadly targets executive functioning. In response to Reviewer 1, we therefore examined task-switching demands more closely by adding the interaction term n-back reaction × cognitive load to a model restricted to 1-back and 2-back Dual Task blocks (as there were no n-back reactions in the Reading Only condition). This analysis showed significantly longer reading times in the 2-back than in the 1back condition, both for trials with and without an n-back reaction. Interestingly, the difference between reaction and no-reaction trials was smaller in the 2-back condition (β = -0.132, t(188066.09) = -34.269, p < 0.001), which may simply reflect the general increase in reading time for all trials so that the effect of the button press time decreases in comparison to the 1-back. In that sense, these findings are not unexpected and largely mirror the main effect of cognitive load. Crucially, however, the three-way interaction of cognitive load, age, and surprisal remained robust (β = 0.00004, t(188198.86) = 3.540, p < 0.001), indicating that our effects cannot be explained by differences in taskswitching costs across load conditions. To maintain a streamlined presentation, we opted not to include this supplementary analysis in the manuscript.

(2) Entropy analyses.

Reviewer 1 pointed out that our initial manuscript placed more emphasis on surprisal. In the revised manuscript, we now report a full set of entropy analyses in the supplementary material. In brief, these analyses show that participants generally benefit from lower entropy across cognitive load conditions, with one notable exception: young adults in the Reading Only condition, where higher entropy was associated with faster reading times. We have added these results to the manuscript to provide a more complete picture of the prediction versus integration distinction highlighted in the review (see sections “Control Analysis: Disentangling the Effect of Cognitive Load on Pre- and PostStimulus Predictive Processing” in the Methods and “Disentangling the Effect of Cognitive Load on Pre- and Post-Stimulus Predictive Processing“ in the Results).

(3) Replication consistency.

Reviewer 1 noted that the results of the replication analysis were somewhat puzzling. We take this point seriously and agree that the original model was likely underpowered to detect the effect of interest. To address this, we excluded the higher-level three-way interaction of age, cognitive load, and surprisal, focusing instead on the primary effect examined in this paper: the modulatory influence of cognitive load on surprisal. Using this approach, we observed highly consistent results between the original online subsample and the online replication sample.

(4) Potential age bias in GPT-2.  

We thank Reviewer 2 for their thoughtful and constructive feedback and agree that a potential age bias in GPT-2’s next-token predictions warrants caution. We thus added a section in the Discussion explicitly considering this limitation, and explain why it should not affect the implications of our study.

Reviewer #1 (Recommendations for the authors):

The d-prime model operates at the block level. How many observation goes into the fitting (about 175*8=1050)? How can the degrees of freedom of a certain variable go up to 188435? 

We thank the reviewer for spotting this issue. Indeed, there was an error in our initial calculations, which we have now corrected in the manuscript. Importantly, the correction does not meaningfully affect the results for the analysis of d-primes or the conclusions of the study (see line 102).  

“A linear mixed-effects model revealed n-back performance declined with cognitive load (β = -1.636, t(173.13) = -26.120, p < 0.001), with more pronounced effects with advancing age (β = -0.014, t(169.77) = -3.931, p > 0.001; Fig. 3b, Table S1)”.

Consider spelling out all the "simple coding schemes" explicitly. 

We thank the reviewer for this helpful suggestion. In the revised manuscript, we have now included the modelled contrasts in brackets after each predictor variable.

“Example from line 527: In both models, we included recording location (online vs. lab), cognitive load (1-back and 2back Dual Task vs. Reading Only as the reference level) and continuously measured age (centred) in both models as well as the interaction of age and cognitive load as fixed effects”.

The relationship between comprehension accuracy and strategies for color judgement is unclear or not intuitive. 

We thank the reviewer for this helpful comment. The n-back task, which required participants to judge colours, was administered at the single-trial level, with colours pseudorandomised to prevent any specific colour - or sequence of colours - from occurring more frequently than others. In contrast, comprehension questions were presented at the end of each block, meaning that trial-level stimulus colour was unrelated to accuracy on the block-level comprehension questions. However, we agree that this distinction may not have been entirely clear, and we have now added a brief clarification in the Methods section to address this point (see line 534):  

“Please note that we did not control for trial-level stimulus colour here. The n-back task, which required participants to judge colours, was administered at the single-trial level, with colours pseudorandomised to prevent any specific colour - or sequence of colours - from occurring more frequently than others. In contrast, comprehension questions were presented at the end of each block, meaning that trial-level stimulus colour was unrelated to accuracy on the blocklevel comprehension questions”.

Could you explain why comprehension accuracy is not modeled in the same way as d-prime, i.e., with a similar set of predictors? 

This is a very good point. After each block, participants answered three comprehension questions that were intentionally designed to be easy: they could all be answered correctly after having read the corresponding text, but not by common knowledge alone. The purpose of these questions was primarily to ensure participants paid attention to the texts and to allow exclusion of participants who failed to understand the material even under minimal cognitive load. As comprehension accuracy was modelled at the block level with 3 questions per block, participants could achieve only discrete scores of 0%, 33.3%, 66.7%, or 100%. Most participants showed uniformly high accuracy across blocks, as expected if the comprehension task fulfilled its purpose. However, this limited variance in performance caused convergence issues when fitting a comprehension-accuracy model at the same level of complexity as the d′ model. To model comprehension accuracy nonetheless, we therefore opted for a reduced model complexity in this analysis.

RT of previous word: The motivations described in the Methods, such as post-error-slowing and sequential modulation effects, lack supporting evidence. The actual scope of what this variable may account for is unclear.  

We are happy to elaborate further regarding the inclusion of this predictor. Reading times, like many sequential behavioral measures, exhibit strong autocorrelation (Schuckart et al., 2025, doi: 10.1101/2025.08.19.670092). That is, the reading time of a given word is partially predictable from the reading time of the previous word(s). Such spillover effects can confound attempts to isolate trialspecific cognitive processes. As our primary goal was to model single-word prediction, we explicitly accounted for this autocorrelation by including the log reading time of the preceding trial as a covariate. This approach removes variance attributable to prior behavior, ensuring that the estimated effects reflect the influence of surprisal and cognitive load on the current word, rather than residual effects of preceding trials. We now added this explanation to the manuscript (see line 553):

“Additionally, it is important to consider that reading times, like many sequential behavioural measures, exhibit strong autocorrelation (Schuckart et al., 2025), meaning that the reading time of a given word is partially predictable from the reading time of the previous word. Such spillover effects can confound attempts to isolate trial-specific cognitive processes. As our primary goal was to model single-word prediction, we explicitly accounted for this autocorrelation by including the reading time of the preceding trial as a covariate”.  

Block-level d-prime: It was shown with the d-prime performance model that block-level d-prime is a function of many of the reading-related variables. Therefore, it is not justified to use them here as "a proxy of each participant's working memory capacity."

We thank the reviewer for their comment. We would like to clarify that the d-prime performance model indeed included only dual-task d-primes (i.e., d-primes obtained while participants were simultaneously performing the reading task). In contrast, the predictor in question is based on singletask d-primes, which are derived from the n-back task performed in isolation. While dual- and singletask d-primes may be correlated, they capture different sources of variance, justifying the use of single-task d-primes here as a measure of each participant’s working memory capacity.

Word frequency is entangled with entropy and surprisal. Suggest removal.

We appreciate the reviewer’s comment. While word frequency is correlated with word surprisal, its inclusion does not affect the interpretation of the other predictors and does not introduce any bias. Moreover, it is a theoretically important control variable in reading research. Since we are interested in the effects of surprisal and entropy beyond potential biases through word length and frequency, we believe these are important control variables in our model. Moreover, checks for collinearity confirmed that word frequency was neither strongly correlated with surprisal nor entropy. In this sense, including it is largely pro forma: it neither harms the model nor materially changes the results, but it ensures that the analysis appropriately accounts for a well-established influence on word processing.

Entropy reflects the cognitive load of word prediction. It should be investigated in parallel and with similar depth as surprisal (which reflects the load of integration).

This is an excellent point that warrants further investigation, especially since the previous literature on the effects of entropy on reading time is scarce and somewhat contradictory. We have thus added additional analyses and now report the effects of cognitive load, entropy, and age on reading time (see sections “Disentangling the Effect of Cognitive Load on Pre- and Post-Stimulus Predictive Processing” in the Results, “Control Analysis: Disentangling the Effect of Cognitive Load on Pre- and Post-Stimulus Predictive Processing” in the Methods as well as Fig. S7 and Table S6 in the Supplements for full results). In brief, we observe a significant three-way interaction among age, cognitive load, and entropy. Specifically, while all participants benefit from low entropy under high cognitive load, reflected by shorter reading times, in the baseline condition this benefit is observed only in older adults. Interestingly, in the baseline condition with minimal cognitive load, younger adults even show a benefit from high entropy. Thus, although the overall pattern for entropy partly mirrors that for surprisal – older adults showing increased reading times when word entropy is high and generally greater sensitivity to entropy variations – the effects differ in one important respect. Unlike for surprisal, the detrimental impact of increased word entropy is more pronounced under high cognitive load across all participants.

Reviewer #2 (Recommendations for the authors):

I agree in relation to prediction/load, but I am concerned (actually very concerned) that prediction needs to be assessed with respect to age. I suspect this is one reason why there is so much inconsistency in the effects of age in prediction and, indeed, comprehension more generally. I think the authors should either deal with it appropriately or drop it from the manuscript.

Thank you for raising this important concern. It is true that prediction is a highly individual, complex process as it depends upon the experiences a person has made with language over their lifespan. As such, one-size-fits-all approaches are not sufficient to model predictive processing. In our study, we thus took particular care to ensure that our analyses captured both age-related and other interindividual variability in predictive processing.

First, in our statistical models, we included age not only as a nuisance regressor, but also assessed age-related effects in the interplay of surprisal and cognitive load. By doing so, we explicitly model potential age-related differences in how individuals of different ages predict language under different levels of cognitive load.

Second, we hypothesised that predictive processing might also be influenced by a range of interindividual factors beyond age, including language exposure, cognitive ability, and more transient states such as fatigue. To capture such variability, all models included by-subject random intercepts and slopes, ensuring that unmodelled individual differences were statistically accommodated.

Together, these steps allow us to account for both systematic age-related differences and residual individual variability in predictive processing. We are therefore confident that our findings are not confounded by unmodelled age-related variability.

Line 18, do not confuse prediction (or pre-activation) with predictability. Predictability effects can be due to integration difficulty. See Pickering and Gambi 2018 for discussion. The discussion then focuses on graded parallel predictions, but there is also a literature concerned with the prediction of one word, typically using the "visual world" paradigm (which is barely cited - Reference 60 is an exception). In the next paragraph, I would recommend discussing the N400 literature (particularly Federmeier). There are a number of reading time studies that investigate whether there is a cost to a disconfirmed prediction - often finding no cost (e.g., Frisson, 2017, JML), though there is some controversy and apparent differences between ERP and eye-tracking studies (e.g., Staub). This literature should be addressed. In general, I appreciate the value of a short introduction, but it does seem too focused on neuroscience rather than the very long tradition of behavioural work on prediction and predictability.

We thank the reviewer for this suggestion. In the revised manuscript, we have clarified the relevant section of the introduction to avoid confusion between predictability and predictive processing, thereby improving conceptual clarity (see line 16).

“Instead, linguistic features are thought to be pre-activated broadly rather than following an all-or-nothing principle, as there is evidence for predictive processing even for moderately- or low-restraint contexts (Boston et al., 2008; Roland et al., 2012; Schmitt et al., 2021; Smith & Levy, 2013)”.  

We also appreciate the reviewer’s comment regarding the introduction. While our study is behavioural, we frame it in a neuroscience context because our findings have direct implications for understanding neural mechanisms of predictive processing and cognitive load. We believe that this framing is important for situating our results within the broader literature and highlighting their relevance for future neuroscience research.

I don't think 2 two-word context is enough to get good indicators of predictability. Obviously, almost anything can follow "in the", but the larger context about parrots presumably gives a lot more information. This seems to me to be a serious concern - or am I misinterpreting what was done? 

This is a very important point and we thank the reviewer for raising it. Our goal was to generate word surprisal scores that closely approximate human language predictions. In the manuscript, we report analyses using a 2-word context window, following recommendations by Kuribayashi et al. (2022).

To evaluate the impact of context length, we also tested longer windows of up to 60 words (not reported). While previous work (Goldstein et al., 2022) shows that GPT-2 predictions can become more human-like with longer context windows, we found that in our stimuli – short newspaper articles of only 300 words – surprisal scores from longer contexts were highly correlated with the 2word context, and the overall pattern of results remained unchanged. To illustrate, surprisal scores generated with a 10-word context window and surprisal scores generated with the 2-word context window we used in our analyses correlated with Spearman’s ρ = 0.976.

Additionally, on a more technical note, using longer context windows reduces the number of analysable trials, since surprisal cannot be computed for the first k words of a text with a k-word context window (e.g., a 50-word context would exclude ~17% of the data).  

Importantly, while a short 2-word context window may introduce additional noise in the surprisal estimates, this would only bias effects toward zero, making our analyses conservative rather than inflating them. Critically, the observed effects remain robust despite this conservative estimate, supporting the validity of our findings.

However, we agree that this is a particularly important and sensitive point, and have now added a discussion of it to the manuscript (see line 476).

“Entropy and surprisal scores were estimated using a two-word context window. While short contexts have been shown to enhance GPT-2’s psychometric alignment with human predictions, making next-word predictions more human-like (Kuribayashi et al., 2022), other work suggests that longer contexts can also increase model–human similarity (Goldstein et al., 2022). To reconcile these findings in our stimuli and guide the choice of context length, we tested longer windows and found surprisal scores were highly correlated with the 2-word context (e.g., 10-word vs. 2-word context: Spearman’s ρ = 0.976), with the overall pattern of results unchanged. Additionally, employing longer context windows would have also reduced the number of analysable trials, since surprisal cannot be computed for the first k words of a text with a k-word context window. Crucially, any additional noise introduced by the short context biases effect estimates toward zero, making our analyses conservative rather than inflating them”.

Line 92, task performance, are there interactions? Interactions would fit with the experimental hypotheses. 

Yes, we did include an interaction term of age and cognitive load and found significant effects on nback task performance (d-primes; b = -0.014, t(169.8) = -3.913, p < 0.001), but not on comprehension question accuracy (see table S1 and Fig. S2 in the supplementary material).

Line 149, what were these values?

We found surprisal values ranged between 3.56 and 72.19. We added this information in the manuscript (see line 143).

Author response:

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

Reviewer #1 (Public review):

The authors used fluorescence microscopy, image analysis, and mathematical modeling to study the effects of membrane affinity and diffusion rates of MinD monomer and dimer states on MinD gradient formation in B. subtilis. To test these effects, the authors experimentally examined MinD mutants that lock the protein in specific states, including Apo monomer (K16A), ATP-bound monomer (G12V), and ATPbound dimer (D40A, hydrolysis defective), and compared to wild-type MinD. Overall, the experimental results support the conclusion that reversible membrane binding of MinD is critical for the formation of the MinD gradient, but that the binding affinities between monomers and dimers are similar.  

The modeling part is a new attempt to use the Monte Carlo method to test the conditions for the formation of the MinD gradient in B. subtilis. The modeling results provide good support for the observations and find that the MinD gradient is sensitive to different diffusion rates between monomers and dimers. This simulation is based on several assumptions and predictions, which raises new questions that need to be addressed experimentally in the future. However, the current story is sufficient without testing these assumptions or predictions.

Reviewer #2 (Public review): 

Summary:  

Bohorquez et al. investigate the molecular determinants of intracellular gradient formation in the B. subtilis Min system. To this end, they generate B. subtilis strains that express MinD mutants that are locked in the monomeric or dimeric states, and also MinD mutants with amphipathic helices of varying membrane affinity. They then assess the mutants' ability to bind to the membrane and form gradients using fluorescence microscopy in different genetic backgrounds. They find that, unlike in the E. coli Min system, the monomeric form of MinD is already capable of membrane binding. They also show that MinJ is not required for MinD membrane binding and only interacts with the dimeric form of MinD. Using kinetic

Monte Carlo simulations, the authors then test different models for gradient formation, and find that a MinD gradient along the cell axis is only formed when the polarly localized protein MinJ stimulates dimerization of MinD, and when the diffusion rate of monomeric and dimeric MinD differs. They also show that differences in the membrane affinity of MinD monomers and dimers are not required for gradient formation.  

Strengths:  

The paper offers a comprehensive collection of the subcellular localization and gradient formation of various MinD mutants in different genetic backgrounds. In particular, the comparison of the localization of these mutants in a delta MinC and MinJ background offers valuable additional insights. For example, they find that only dimeric MinD can interact with MinJ. They also provide evidence that MinD locked in a dimer state may co-polymerize with MinC, resulting in a speckled appearance.  

The authors introduce and verify a useful measure of membrane affinity in vivo.  

The modulation of the membrane affinity by using distinct amphipathic helices highlights the robustness of the B. subtilis MinD system, which can form gradients even when the membrane affinity of MinD is increased or decreased.  

Weaknesses:  

The main claim of the paper, that differences in the membrane affinity between MinD monomers and dimers are not required for gradient formation, does not seem to be supported by the data. The only measure of membrane affinity presented is extracted from the transverse fluorescence intensity profile of cells expressing the mGFP-tagged MinD mutants. The authors measure the valley-to-peak ratio of the profile, which is lower than 1 for proteins binding to the membrane and higher than 1 for cytosolic proteins. To verify this measure of membrane affinity, they use a membrane dye and a soluble GFP, which results in values of ~0.75 and ~1.25, respectively. They then show that all MinD mutants have a value - roughly in the range of 0.8-0.9 - and they use this to claim that there are no differences in membrane affinity between monomeric and dimeric versions.  

While this way to measure membrane affinity is useful to distinguish between binders and non-binders, it is unclear how sensitive this assay is, and whether it can resolve more subtle differences in membrane affinity, beyond the classification into binders and non-binders. A dimer with two amphipathic helices should have a higher membrane affinity than a monomer with only one such copy. Thus, the data does not seem to support the claim that "the different monomeric mutants have the same membrane affinity as the wildtype MinD". The data only supports the claim that B. subtilis MinD monomers already have a measurable membrane affinity, which is indeed a difference from the E. coli Min system.  

While their data does show that a stark difference between monomer and dimer membrane affinity may not be required for gradient formation in the B. subtilis case, it is also not prevented if the monomer is unable to bind to the membrane. They show this by replacing the native MinD amphipathic helix with the weak amphipathic helix NS4AB-AH. According to their membrane affinity assay, NS4AB-AH does not bind to the membrane as a monomer (Figure 4D), but when this helix is fused to MinD, MinD is still capable of forming a gradient (albeit a weaker one). Since the authors make a direct comparison to the E. coli MinDE systems, they could have used the E. coli MinD MTS instead or in addition to the NS4AB-AH amphipathic helix. The reviewer suspects that a fusion of the E. coli MinD MTS to B. subtilis MinD may also support gradient formation.  

The paper contains insufficient data to support the many claims about cell filamentation and minicell formation. In many cases, statements like "did not result in cell filamentation" or "restored cell division" are only supported by a single fluorescence image instead of a quantitative analysis of cell length distribution and minicell frequency, as the one reported for a subset of the data in Figure 5.  

The paper would also benefit from a quantitative measure of gradient formation of the distinct MinD mutants, instead of relying on individual fluorescent intensity profiles.  

The authors compare their experimental results with the oscillating E. coli MinDE system and use it to define some of the rules of their Monte Carlo simulation. However, the description of the E. coli Min system is sometimes misleading or based on outdated findings.

The Monte Carlo simulation of the gradient formation in B. subtilis could benefit from a more comprehensive approach:

(1) While most of the initial rules underlying the simulation are well justified, the authors do not implement or test two key conditions:

(a) Cooperative membrane binding, which is a key component of mathematical models for the oscillating E. coli Min system. This cooperative membrane binding has recently been attributed to MinD or MinCD oligomerization on the membrane and has been experimentally observed in various instances; in fact, the authors themselves show data supporting the formation of MinCD copolymers.  

(2) Local stimulation of the ATPase activity of MinD which triggers the dimer-to-monomer transition; E. coli MinD ATP hydrolysis is stimulated by the membrane and by MinE, so B. subtilis MinD may also be stimulated by the membrane and/or other components like MinJ. Instead, the authors claim that (a) would only increase differences in diffusion between the monomer and different oligomeric species, and that a 2-fold increase in dimerization on the membrane could not induce gradient formation in their simulation, in the absence of MinJ stimulating gradient formation. However, a 2-fold increase in dimerization is likely way too low to explain any cooperative membrane binding observed for the E. coli Min system. Regarding (b), they also claim that implementing stimulation of ATP hydrolysis on the membrane (dimer-to-monomer transition) would not change the outcome, but no simulation result for this condition is actually shown.  

(3) To generate any gradient formation, the authors claim that they would need to implement stimulation of dimer formation by MinJ, but they themselves acknowledge the lack of any experimental evidence for this assertion. They then test all other conditions (e.g., differences in membrane affinity, diffusion, etc.) in addition to the requirement that MinJ stimulates dimer formation. It is unclear whether the authors tested all other conditions independently of the "MinJ induces dimerization" condition, and whether either of those alone or in combination could also lead to gradient formation. This would be an important test to establish the validity of their claims.

Reviewer #3 (Public review): 

This important study by Bohorquez et al examines the determinants necessary for concentrating the spatial modulator of cell division, MinD, at the future site of division and the cell poles. Proper localization of MinD is necessary to bring the division inhibitor, MinC, in proximity to the cell membrane and cell poles where it prevents aberrant assembly of the division machinery. In contrast to E. coli, in which MinD oscillates from pole to pole courtesy of a third protein MinE, how MinD localization is achieved in B. subtilis - which does not encode a MinE analog - has remained largely a mystery. The authors present compelling data indicating that MinD dimerization is dispensable for membrane localization but required for concentration at the cell poles. Dimerization is also important for interactions between MinD and MinC, leading to the formation of large protein complexes. Computational modeling, specifically a Monte Carlo simulation, supports a model in which differences in diffusion rates between MinD monomers and dimers lead to the concentration of MinD at cell poles. Once there, interaction with MinC increases the size of the complex, further reinforcing diffusion differences. Notably, interactions with MinJ-which has previously been implicated in MinCD localization, are dispensable for concentrating MinD at cell poles although MinJ may help stabilize the MinCD complex at those locations.  

Reviewer #1 (Recommendations for the authors):  

(1) The title could be modified to better reflect the emphasis on MinD monomer and dimer diffusion rather than the fact that membrane affinity is not important in MinD gradient formation. In addition, because membrane association requires affinity for the membrane, this title seems inconsistent with statements in the main text, such as Lines 246-247: a reversible membrane association is important for the formation of a MinD gradient along the cell axis.

We agree with the reviewer that the title can be more accurate, and we have now changed it to “Membrane affinity difference between MinD monomer and dimer is not crucial to MinD gradient formation in Bacillus subtilis”

(2) This paper reports that the difference in diffusion rates between MinD monomers and dimers is an important factor in the formation of Bs MinD gradients. However, one can argue for the importance of MinD monomers in the cellular context. Since the abundance of ATP in cells often far exceeds the abundance of MinD protein molecules under experimental conditions, MinD can easily form dimers in the cytoplasm. How does the author address this problem?  

It is a good point that ATP concentration in the cell likely favours dimers in the cytoplasm. However, what is important in our model is that there is cycling between monomer and dimer, rather than where exactly this happen. In fact, the gradients works essentially equally well if dimers can become monomers only whilst they are at the membrane, as we have mentioned in the manuscript (lines 324-326 in the original manuscript). However, in the original manuscript this simulation was not shown, and now we have included this in the new Fig. 8D & E.

(3)The claim "This oscillating gradient requires cycling of MinD between a monomeric cytosolic and a dimeric membrane attached state." (Lines 46, 47) is not well supported by most current studies and needs to be revised since to my knowledge, most proposed models do not consider the monomer state. The basic reaction steps of Ec Min oscillations include ATP-bound MinD dimers attaching to the membrane that subsequently recruit more MinD dimers and MinE dimers to the membrane; MinE interactions stimulate ATP hydrolysis in MinD, leading to dissociation of ADP-bound MinD dimers from the membrane; nucleotide exchange occurs in the cytoplasm.  

Here the reviewer refers to a sentence in a short “Importance” abstract that we have added. In fact, such abstract is not necessary, so we have removed it. Of note, the E. coli MinD oscillation, including the role of MinE, is described in detail in the Introduction. 

A recent reference is a paper by Heermann et al. (2020; doi: 10.1016/j.jmb.2020.03.012), which considers the MinD monomer state, which is not mentioned in this work. How do their observations compare to this work?  

The Heermann paper mentions that MinD bound to the membrane displays an interface for multimerization, and that this contributes to the local self-enhancement of MinD at the membrane. In our Discussion, we do mention that E. coli MinD can form polymers in vitro and that any multimerization of MinD dimers will further increase the diffusion difference between monomer and dimer, and might contribute to the formation of a protein gradient (lines 459-467). We have now included a reference to the Heermann paper (line 461).

(4) Throughout the manuscript, errors in citing references were found in several places.                 

We have corrected this where suggested.

(5) The introduction may be somewhat misleading due to mixed information from experimental cellular results, in vitro reconstructions, and theoretical models in cells or in vitro environments. Some models consider space constraints, while others do not. Modifications are recommended to clarify differences.  

See below for responses 

(6) The citation for MinD monomers:

The paper by Hu and Lutkenhaus (2003, doi: 10.1046/j.1365-2958.2003.03321.x.) contains experimental evidence showing monomer-dimer transition using purified proteins. Another paper by the same laboratory (Park et al. 2012, doi: 10.1111/j.1365-2958.2012.08110.x.) explained how ATP-induced dimerization, but this paper is not cited.  

The Park et al. 2012 paper focusses at the asymmetric activation of MinD ATPase by MinE, which goes beyond the scope of our work. However, we have cited several other papers from the Lutkenhaus lab, including the Wu et al. 2011 paper describing the structure of the MinD-ATP complex.

Other evidence comes from structural studies of Archaea Pyrococcus furiosus (1G3R) and Pyrococcus horikoshii (1ION), and thermophilic Aquifex aeolicus (4V01, 4V02, 4V03). As they may function differently from Ec MinD, they are less relevant to this manuscript.

We agree. 

(7) Lines 65, 66: Using the term 'a reaction-diffusion couple' to describe the biochemical facts by citing references of Hu and Lutkenhaus (1999) and Raskin and de Boer (1999) is not appropriate. The idea that the Min system behaves as a reaction-diffusion system was started by Howard et al. (2001), Meinhardt and de Boer (2001), and Huang et al. (2003) et al. In addition, references for MinE oscillation are missing. 

We have now corrected this (line 52).

(8) Lines 77-79: Citations are incorrect.

ATP-induced dimerization: Hu and Lutkenhaus (2003, DOI: 10.1046/j.1365-2958.2003.03321.x), Park et al. (2012). C-terminal amphipathic helix formation: Szeto et al. (2003), Hu and Lutkenhaus (2003, DOI: 10.1046/j.1365-2958.2003.03321.x).

Citations have been corrected.

(9) Line 78: The C-terminal amphipathic helix is not pre-formed and then exposed upon conformational change induced by ATP-binding. This alpha-helical structure is an induced fold upon interaction with membranes as experimentally demonstrated by Szeto et al. (2003).  

We have adjusted the text to correct this (lines 64-66).

(10) Line 102: 'cycles between membrane association and dissociation of MinD' also requires MinE in addition to ATP.

We believe that in the context of this sentence and following paragraph it is not necessary to again mention MinE, since it is focused on parallels between the E. coli and B. subtilis MinD membrane binding cycles.

(11) In the introduction, could the author briefly explain to a general audience the difference between Monte Carlo and reaction-diffusion methods? How do different algorithms affect the results?

The main difference between the kinetic Monte Carlo and typical reaction-diffusion methods which is relevant to our work is that the first is particle-based, and naturally includes statistical fluctuations (noise), whereas the second is field-based, and is in the normal implementation deterministic, so does not include noise. Whilst it should be noted that one can in principle include noise in the field-based reactiondiffusion methods, this is done rarely. Additionally, although we do not do this here, the kinetic MonteCarlo can also account, in principle, for particle shape (sphere versus rod), or for localized interactions (as sticky patches on the surface): therefore the kinetic Monte Carlo is more microscopic in nature. We have now shortly described the difference in lines 102-105.

(12)  Lines 126-128: The second part of the sentence uses the protein structure of Pyrococcus furiosus MinD (Ref 37) to support a protein sequence comparison between Ec and Bs MinD. However, the structure of the dimeric E. coli MinD-ATP complex (3Q9L) is available, which is Reference 38 that is more suited for direct comparison.

To discuss monomeric MinD from P. furiosus, it will be useful to include it in the primary sequence alignment in Figure S1.

We do not think that this detailed information is necessary to add to Figure S1, since the mutants have been described before (appropriate citations present in the text).

(13) Lines 127, 166: Where Figure S1 is discussed, a structural model of MinD will be useful alongside with the primary sequence alignment.

We do not think that this detailed information is necessary to understand the experiments since the mutants have been described before.

(14) Lines 131-132: Reference is missing for the sentence of " the conserved..."; Reference 38.  In Reference 38, there is no experimental evidence on G12 but inferred from structure analysis. Reference 26 discusses ATP and MinE regulation on the interactions between MinD and phospholipid bilyers; not about MinD dimerization.

We have corrected this and added the proper references. 

For easy reading, the mutant MinD phenotypes can be indicated here instead of in the figure legends, including K16A (apo monomer), MinD G12V (ATP-bound monomer), and MinD D40A (ATP-bound dimer, ATP hydrolysis deficient).  

We have added the suggested descriptions of the mutants in the main text.

(15) Lines 150-151: Unlike Ec MinD, which forms a clear gradient in one half of the cell, Bs MinD (wild type) mainly accumulates at the hemispheric poles. What percentage of a cell (or cell length) can be covered by the Bs MinD gradient? How does the shaded area in the longitudinal FIP compare to the area of the bacterial hemispherical pole? If possible, it might be interesting to compare with the range of nucleoid occlusion mechanisms that occur.

Part of the MinD gradient covers the nucleoid area, since the fluorescence signal is still visible along the cell lengths, yet there is no sudden drop in fluorescence, suggesting that nucleoid exclusion does not play a role.

(16)  Line 160: In addition to summarizing the membrane-binding affinity, descriptions of the differences in the gradient distribution or formation will be useful.  

We have done this in lines 155-156 of the original manuscript: “The monomeric ATP binding G12V variant shows the same absence of a protein gradient as the K16A variant”.

(17) Line 262: 'distribution' is not shown.  

We do not understand this remark. This information is shown in Fig. 5B (now Fig. 6B).

(18)  Line 287: Wrong citation for reference 31.

Reference has been corrected.

(19)  Line 288 and lines 596 regarding the Monte Carlo simulation:

(a)  An illustration showing the reaction steps for MinD gradient formation will help understand the rationale and assumptions behind this simulation.

We have added an illustration depicting the different modelling steps in the new Fig. 8.

(b)  Equations are missing.

(c)   A table summarizing the parameters used in the simulation and their values.

(d)  For general readers, it will be helpful to convert the simulation units to real units.

(e)  Indicate real experimental data with a citation or the reason for any speculative value.

The Methods section provides a discussion of all parameters used in the potentials on which our kinetic Monte-Carlo algorithm is based. We have now also provided a Table in the SI (Table S1) with typical parameter values in both simulation units and real units. The experimental data and reasoning behind the values chosen are discussed in the Methods section (see “Kinetic Monte Carlo simulation”).

(20)  Lines 320-321: Reference missing.

The interaction between MinJ and the dimer form of MinD is based on our findings shown in the original Fig. S4, and this information has not been published before. We have rephrased the sentence to make it more clear. Of note, Fig. S4 has been moved to the main manuscript, at the request of reviewer #2, and is now new Fig. 2. 

(21)  Lines 355-359: Is the statement specifically made for the Bs Min system? Is there any reference for the statement? Isn't the differences in diffusion rates between molecules 'at different locations' in the system more important than reducing their diffusion rates alone? It is unclear about the meaning of the statement "the Min system uses attachment to the membrane to slow down diffusion". Is this an assumption in the simulation?

The statement is generic, however the reviewer has a good point and we have made this statement more clear by changing “considerably reduced diffusion rate” to “locally reduced diffusion rate” (line 359).

(22) Line 403: Citation format.

We have corrected the text and citation.

(23) Lines 442-444: The parameters are not defined anywhere in the manuscript.

Discussed in the M&M and in the new Table S1.

(24) Lines 464-465: Regarding the final sentence, what does 'this prediction' refer to? Hasn't the author started with experimental observations, predicted possible factors of membrane affinity and diffusion rates, and used the simulation approach to disapprove or support the prediction?

We have changed “prediction” to “suggestion”, to make it clear that it is related to the suggestion in the previous sentence that  “our modelling suggests that stimulation of MinD-dimerization at cell poles and cell division sites is needed.” (line 471).

(25) Materials and Methods: Statistical methods for data analyses are missing.

Added to “Microscopy” section.

(26) References: References 34, 40, 51 are incomplete.

References 34 and 40 have been corrected. Reference 51 is a book.

(27)  Figures: The legends (Figures 1-7) can be shortened by removing redundant details in Material and Methods. Make sure statistical information is provided. The specific mutant MinD states, including Apo monomer, ATP-bound dimer, ATP hydrolysis deficient, and non-membrane binding etc can be specified in the main text. They are repeated in the legends of Figures 1 and 2.

We have removed redundant details from the legends and provided statistical information.

(28)  Supporting information:

Table S1: Content of the acknowledgment statement may be moved to materials and methods and the acknowledgment section. Make sure statistical information is provided in the supporting figure legends.

We are not sure what the reviewer means with the content acknowledgement in Table S1 (now Table S2). Statistical information has been added.

Figure S1. Adding a MinD structure model will be useful.

We do not think that a structural model will enlighten our results since our work is not focused at structural mutagenesis. The mutants that we use have been described in other papers that we have cited.

Reviewer #2 (Recommendations for the authors):  

The authors should cite and relate their data to the preprint by Feddersen & Bramkamp, BioRxiv 2024. ATPase activity of B. subtilis MinD is activated solely by membrane binding.

We have now discussed this paper in relation to our data in lines 407-409. 

I am not convinced the authors are able to make the statement in lines 160-161 based on their assay: "This confirmed that the different monomeric mutants have the same membrane affinity as wild-type MinD". It is unclear if measuring valley-to-peak ratios in their longitudinal profiles can resolve small differences in membrane affinity. Wildtype MinD should at least be dimeric, or (as the authors also note elsewhere) may even be present in higher-order structures and as such have a higher membrane affinity than a monomeric MinD mutant. The authors should rephrase the corresponding sections in the manuscript to state that the MinD monomer already has detectable membrane affinity, instead of stating that the monomer and dimer membrane affinity are the same.

We agree that “the same affinity” is too strongly worded, and we have now rephrased this by saying that the different monomeric mutants have a comparable membrane affinity as wild type MinD (line 152).

According to the authors' analysis, MinD-NS4B would not bind to the membrane as it has a valley-to-peak ratio higher than 1, similar to the soluble GFP. However, the protein is clearly forming a gradient, and as such probably binding to the membrane. The authors should discuss this as a limitation of their membrane binding measure.

The ratio value of 1 is not a cutoff for membrane binding. As shown in Fig. 1F, GFP has a valley-topeak ratio close to 1.25, whereas the FM5-95 membrane dye has a ratio close to 0.75. In Fig. 3C (now Fig. 4C) we have shown that GFP fused with the NS4B membrane anchor has a lower ratio than free GFP, and we have shown the same in Fig. 4D (now Fig. 5D) for GFP-MinD-NS4B. The difference are small but clear, and not similar to GFP.

The observation that MinD dimers are localized by MinJ is interesting and key to the rule of the Monte Carlo simulation that dimers attach to MinJ. However, the data is hidden in the supplementary information and is not analysed as comprehensively, e.g., it lacks the analysis of the membrane binding. The paper would benefit from moving the fluorescence images and accompanying analysis into the main text.  

We have moved this figure to the main text and added an analysis of the fluorescence intensities (new Fig. 2).

The authors should show the data for cell length and minicell formation, not only for the MinDamphipathic helix versions (Fig. 5), but also for the GFP-MinD, and all the MinD mutants. They do refer to some of this data in lines 145-148 but do not show it anywhere. They also refer to "did not result in cell filamentation" in line 213 and to "resulted in highly filamentous cells" and "Introduction of a minC deletion restored cell division" in lines 167-160 without showing the cell length and minicell data, but instead refer to the fluorescence image of the respective strain. I would suggest the authors include this data either in a subpanel in the respective figure or in the supplementary information.

The effect of uncontrolled MinC activity is very apparent and leads to long filamentous cells. Also the occurrence of minicells is apparent. Cell lengths distribution of wild type cells is shown in Fig. 6B, and minicell formation is negligibly small in wild type cells.

The transverse fluorescence intensity profiles used as a measure for membrane binding are an average profile from ~30 cells. In the case of the longitudinal profiles that display the gradient, only individual profiles are displayed. I understand that because of distinct cell length, the longitudinal profiles cannot simply be averaged. However, it is possible to project the profiles onto a unit length for averaging (see for example the projection of profiles in McNamara. et al., BioRxiv (2023)). It would be more convincing to average these profiles, which would allow the authors to also quantify the gradients in more detail. If that is impossible, the authors may at least quantify individual valley-to-peak ratios of the longitudinal fluorescence profiles as a measure of the gradient.

We agree that in future work it would be better to average the profiles as suggested. However, due to limited time and resources, we cannot do this for the current manuscript.

Regarding the rules and parameters used for the Monte Carlo simulation (see also the corresponding sections in the public review):

(1) The authors mention that they have not included multimerization of MinD in their simulation but argue in the discussion that it would only strengthen the differences in the diffusion between monomers and multimers. This is correct, but it may also change the membrane residence time and membrane affinity drastically.

Simulation of multimerization is difficult, but we have now included a simulation whereby MinD dimers can also form tetramers (lines 341-348), shown in the new Fig. 8K. This did not alter the MinD gradient much. 

(2) The authors implement a dimer-to-monomer transition rate that they equate with the stochastic ATP hydrolysis rate occurring with a half-life of approximately 1/s (line 305). They claim that this rate is based on information from E. coli and cite Huang and Wingreen. However, the Huang paper only mentions the nucleotide exchange rate from ADP to ATP at 1/s. Later that paper cites their use of an ATP hydrolysis rate of 0.7/s to match the E. coli MinDE oscillation rate of 40s. From the authors' statement, it is unclear to me whether they refer to the actual ATP hydrolysis rate in Huang and Wingreen or something else. For E. coli MinD, both the membrane and MinE stimulate ATPase activity. Even if B. subtilis lacks MinE, ATP hydrolysis may still be stimulated by the membrane, which has also been reported in another preprint (Feddersen & Bramkamp, BioRxiv 2024). It may also be stimulated by other components of the Min system like MinJ. The authors should include in the manuscript the Monte Carlo simulation implementing dimer to monomer transition on the membrane only, which is currently referred to only as "(data not shown)". 

The exact value of the ATP hydrolysis rate is not so important here, so 1/s only gives the order of magnitude (in line with 0.7/s above), which we have now clarified in lines 631-632. We have now also added the “(data not shown” results to Fig. 8, i.e. simulations where dimer to monomer transitions (i.e. ATPase activity) only occurs at the membrane (Fig. 8D & E, and lines 319-322).

(3) How long did the authors simulate for? How many steps? What timesteps does the average pictured in Figure 7 correspond to?

We simulated 10^7time steps (corresponding to 100 s in real time). We have checked that the simulation steps for which we average are in steady state. Typical snapshots are recorded after 10^610^7time steps, when the system is in steady state. We have added this information in lines 299-300.

There are several misconceptions about the (oscillating E. coli) Min system in the main text:

(1) Lines 77-78: "In case of the E. coli MinD, ATP binding leads to dimerization of MinD, which induces a conformational change in the C-terminal region, thereby exposing an amphiathic helix that functions as a membrane binding domain" and "This shows a clear difference with the E. coli situation, where dimerization of MinD causes a conformational change of the C-terminal region enabling the amphipathic helix to insert into the lipid bilayer" in lines 400-403 are incorrect. There is no evidence that the amphipathic helix at the C-terminus of MinD changes conformation upon ATP binding; several studies have shown instead that a single copy of the amphipathic helix is too weak to confer efficient membrane binding but that the dimerization confers increased membrane binding as now two amphipathic helices are present leading to an avidity effect in membrane binding. Please refer to the following papers (Szeto et al., JBC (2003); Wu et al., Mol Microbiol (2011); Park et al., Cell (2011); Heermann et al., JMB (2020); Loose et al., Nat Struct Mol Biol (2011); Kretschmer et al., ACS Syn Biol (2021); Ramm et al., Nat Commun (2018) or for a better overview the following reviews on the topic of the E. coli Min system Wettmann and Kruse, Philos Trans R Soc B Biol (2018), Ramm et al., Cell and Mol Life Sci (2019); Halatek et al., Philos Trans R SocB Biol Sci (2018).

This is indeed incorrectly formulated, and we have now amended this in lines 64-66 and lines 403406. Key papers are cited in the text.

(2) The authors mention that E. coli MinD may multimerize, citing a study where purified MinD was found to polymerize, and then suggest that this is unlikely to be the case in B. subtilis as FRAP recovery of MinD is quick. However, cooperativity in membrane binding is essential to the mathematical models reproducing E. coli Min oscillations, and there is more recent experimental evidence that E. coli MinD forms smaller oligomers that differ in their membrane residence time and diffusion (e.g., Heermann et al., Nat Methods (2023); Heermann et al., JMB (2020);) I would suggest the authors revise the corresponding text sections and test the multimerization in their simulation (see above).

As mentioned above, simulating oligomerization is difficult, but in order to approximate related cooperative effects, we have simulated a situation whereby MinD dimers can form tetramers. This simulation did not show a large change in MinD gradient formation. We have added the result of this simulation to Fig. 8 (Fig. 8K), and discuss this further in lines 341-348 and 459-467.

(3) Lines 75-76 and lines 79-80: The sentences "MinC ... and needs to bind to the Walker A-type ATPase MinD for its activity" and "The MinD dimer recruits MinC ... and stimulates its activity" are misleading. MinC is localized by MinD, but MinD does not alter MinC activity, as MinC mislocalization or overexpression also prevents FtsZ ring formation leading to minicell or filamentous cells, as also later described by the authors (line 98). There is also no biochemical evidence that the presence of MinD somehow alters MinC activity towards FtsZ other than a local enrichment on the membrane. I would rephrase the sentence to emphasize that MinD is only localizing MinC but does not alter its activity.   

We have rephrased this sentence to prevent misinterpretation (lines 66-67).

Minor points:  

(1)  I am not quite sure what the experiment with the CCCP shows. The authors explain that MinD binding via the amphipathic helix requires the presence of membrane potential and that the addition of CCCP disturbs binding. They then show that the MinD with two amphipathic helices is not affected by CCCP but the wildtype MinD is. What is the conclusion of this experiment? Would that mean that the MinD with two amphipathic helices binds more strongly, very differently, perhaps non-physiologically?  

This experiment was “To confirm that the tandem amphipathic helix increased the membrane affinity of MinD”, as mentioned in the beginning of the paragraph (line 224).  

(2) Lines 456-457: Please cite the FRAP experiment that shows a quick recovery rate of MinD.

Reference has been added. 

(3) Figure 4D: It is unclear to me to which condition the p-value brackets point.

This is related to a statistical t-test. We have added this information to the legend of the figure.

(4) Line 111, "in the membrane affinity of the MinD". I think that the "the" before MinD should be removed.  

Corrected

(5) Typo in line 199 "indicting" instead of indicating.

Corrected

(6) Typo in line 220 "reversable" instead of reversible.

Corrected

(7) Lines 279, 284, 905: "Monte-Carlo" should read Monte Carlo.

Corrected

Reviewer #3 (Recommendations for the authors):  

Introduction: As written, the introduction does not provide sufficient background for the uninitiated reader to understand the function of the MinCD complex in the context of assembly and activation of cell division in B. subtilis. The introduction is also quite long and would benefit from condensing the description of the Min oscillation mechanism in E. coli to one or two sentences. While highlighting the role of MinE in this system is important for understanding how it works, it is only needed as a counterpoint to the situation in B. subtilis.

Since the Min system of E. coli is by far the best understood Min system, we feel that it is important to provide detailed information on this system. However, we have added an introductory sentence to explain the key function of the Min system (line 46-48).

Line 248: Increasing MinD membrane affinity increases the frequency of minicells - however it is unclear if cells are dividing too much or if it is just a Min mutant (i.e. occasionally dividing at the cell pole vs the middle)? Cell length measurements should be included to clarify this point (Figures 4 and 5).

This information is presented in Fig. 5B (Cell length distribution), which is now Fig. 6B, indicating that the average cell length increases in the tandem alpha helix mutant, a phenotype that is comparable to a MinD knockout. 

Figure 5: I am a bit confused as to whether increasing MinD affinity doesn't lead to a general block in division by MinCD rather than phenocopying a minD null mutant.

Although the tandem alpha helix mutant has a cell length distribution comparable to a minD knockout, the tandem mutant produces much less minicells then the minD knockout, indicating that there is still some cell division regulation.

Author response:

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

Reviewer #1 (Public review):

Summary

This work performed Raman spectral microscopy at the single-cell level for 15 different culture conditions in E. coli. The Raman signature is systematically analyzed and compared with the proteome dataset of the same culture conditions. With a linear model, the authors revealed correspondence between Raman pattern and proteome expression stoichiometry indicating that spectrometry could be used for inferring proteome composition in the future. With both Raman spectra and proteome datasets, the authors categorized co-expressed genes and illustrated how proteome stoichiometry is regulated among different culture conditions. Co-expressed gene clusters were investigated and identified as homeostasis core, carbon-source dependent, and stationary phase-dependent genes. Overall, the authors demonstrate a strong and solid data analysis scheme for the joint analysis of Raman and proteome datasets.

Strengths and major contributions

(1) Experimentally, the authors contributed Raman datasets of E. coli with various growth conditions.

(2) In data analysis, the authors developed a scheme to compare proteome and Raman datasets. Protein co-expression clusters were identified, and their biological meaning was investigated.

Weaknesses

The experimental measurements of Raman microscopy were conducted at the single-cell level; however, the analysis was performed by averaging across the cells. The author did not discuss if Raman microscopy can used to detect cell-to-cell variability under the same condition.

We thank the reviewer for raising this important point. Though this topic is beyond the scope of our study, some of our authors have addressed the application of single-cell Raman spectroscopy to characterizing phenotypic heterogeneity in individual Staphylococcus aureus cells in another paper (Kamei et al., bioRxiv, doi: 10.1101/2024.05.12.593718). Additionally, one of our authors demonstrated that single-cell RNA sequencing profiles can be inferred from Raman images of mouse cells (Kobayashi-Kirschvink et al., Nat. Biotechnol. 42, 1726–1734, 2024). Therefore, detecting cell-to-cell variability under the same conditions has been shown to be feasible. Whether averaging single-cell Raman spectra is necessary depends on the type of analysis and the available dataset. We will discuss this in more detail in our response to Comment (1) by Reviewer #1 (Recommendation for the authors).

Discussion and impact on the field

Raman signature contains both proteomic and metabolomic information and is an orthogonal method to infer the composition of biomolecules. It has the advantage that single-cell level data could be acquired and both in vivo and in vitro data can be compared. This work is a strong initiative for introducing the powerful technique to systems biology and providing a rigorous pipeline for future data analysis.

Reviewer #2 (Public review):

Summary and strengths:

Kamei et al. observe the Raman spectra of a population of single E. coli cells in diverse growth conditions. Using LDA, Raman spectra for the different growth conditions are separated. Using previously available protein abundance data for these conditions, a linear mapping from Raman spectra in LDA space to protein abundance is derived. Notably, this linear map is condition-independent and is consequently shown to be predictive for held-out growth conditions. This is a significant result and in my understanding extends the earlier Raman to RNA connection that has been reported earlier.

They further show that this linear map reveals something akin to bacterial growth laws (ala Scott/Hwa) that the certain collection of proteins shows stoichiometric conservation, i.e. the group (called SCG - stoichiometrically conserved group) maintains their stoichiometry across conditions while the overall scale depends on the conditions. Analyzing the changes in protein mass and Raman spectra under these conditions, the abundance ratios of information processing proteins (one of the large groups where many proteins belong to "information and storage" - ISP that is also identified as a cluster of orthologous proteins) remain constant. The mass of these proteins deemed, the homeostatic core, increases linearly with growth rate. Other SCGs and other proteins are condition-specific.

Notably, beyond the ISP COG the other SCGs were identified directly using the proteome data. Taking the analysis beyond they then how the centrality of a protein - roughly measured as how many proteins it is stoichiometric with - relates to function and evolutionary conservation. Again significant results, but I am not sure if these ideas have been reported earlier, for example from the community that built protein-protein interaction maps.

As pointed out, past studies have revealed that the function, essentiality, and evolutionary conservation of genes are linked to the topology of gene networks, including protein-protein interaction networks. However, to the best of our knowledge, their linkage to stoichiometry conservation centrality of each gene has not yet been established.

Previously analyzed networks, such as protein-protein interaction networks, depend on known interactions. Therefore, as our understanding of the molecular interactions evolves with new findings, the conclusions may change. Furthermore, analysis of a particular interaction network cannot account for effects from different types of interactions or multilayered regulations affecting each protein species.

In contrast, the stoichiometry conservation network in this study focuses solely on expression patterns as the net result of interactions and regulations among all types of molecules in cells. Consequently, the stoichiometry conservation networks are not affected by the detailed knowledge of molecular interactions and naturally reflect the global effects of multilayered interactions. Additionally, stoichiometry conservation networks can easily be obtained for non-model organisms, for which detailed molecular interaction information is usually unavailable. Therefore, analysis with the stoichiometry conservation network has several advantages over existing methods from both biological and technical perspectives.

We added a paragraph explaining this important point to the Discussion section, along with additional literature.

Finally, the paper built a lot of "machinery" to connect ¥Omega_LE, built directly from proteome, and ¥Omega_B, built from Raman, spaces. I am unsure how that helps and have not been able to digest the 50 or so pages devoted to this.

The mathematical analyses in the supplementary materials form the basis of the argument in the main text. Without the rigorous mathematical discussions, Fig. 6E — one of the main conclusions of this study — and Fig. 7 could never be obtained. Therefore, we believe the analyses are essential to this study. However, we clarified why each analysis is necessary and significant in the corresponding sections of the Results to improve the manuscript's readability.

Please see our responses to comments (2) and (7) by Reviewer #1 (Recommendations for the authors) and comments (5) and (6) by Reviewer #2 (Recommendations for the authors).

Strengths:

The rigorous analysis of the data is the real strength of the paper. Alongside this, the discovery of SCGs that are condition-independent and that are condition-dependent provides a great framework.

Weaknesses:

Overall, I think it is an exciting advance but some work is needed to present the work in a more accessible way.

We edited the main text to make it more accessible to a broader audience. Please see our responses to comments (2) and (7) by Reviewer #1 (Recommendations for the authors) and comments (5) and (6) by Reviewer #2 (Recommendations for the authors).

Reviewer #1 (Recommendations for the authors):

(1) The Raman spectral data is measured from single-cell imaging. In the current work, most of the conclusions are from averaged data. From my understanding, once the correspondence between LDA and proteome data is established (i.e. the matrix B) one could infer the single-cell proteome composition from B. This would provide valuable information on how proteome composition fluctuates at the single-cell level.

We can calculate single-cell proteomes from single-cell Raman spectra in the manner suggested by the reviewer. However, we cannot evaluate the accuracy of their estimation without single-cell proteome data under the same environmental conditions. Likewise, we cannot verify variations of estimated proteomes of single cells. Since quantitatively accurate single-cell proteome data is unavailable, we concluded that addressing this issue was beyond the scope of this study.

Nevertheless, we agree with the reviewer that investigating how proteome composition fluctuates at the single-cell level based on single-cell Raman spectra is an intriguing direction for future research. In this regard, some of our authors have studied the phenotypic heterogeneity of Staphylococcus aureus cells using single-cell Raman spectra in another paper (Kamei et al., bioRxiv, doi: 10.1101/2024.05.12.593718), and one of our authors has demonstrated that single-cell RNA sequencing profiles can be inferred from Raman images of mouse cells (Kobayashi-Kirschvink et al., Nat. Biotechnol. 42, 1726–1734, 2024). Therefore, it is highly plausible that single-cell Raman spectroscopy can also characterize proteomic fluctuations in single cells. We have added a paragraph to the Discussion section to highlight this important point.

(2) The establishment of matrix B is quite confusing for readers who only read the main text. I suggest adding a flow chart in Figure 1 to explain the data analysis pipeline, as well as state explicitly what is the dimension of B, LDA matrix, and proteome matrix.

We thank the reviewer for the suggestion. Following the reviewer's advice, we have explicitly stated the dimensions of the vectors and matrices in the main text. We have also added descriptions of the dimensions of the constructed spaces. Rather than adding another flow chart to Figure 1, we added a new table (Table 1) to explain the various symbols representing vectors and matrices, thereby improving the accessibility of the explanation.

(3) One of the main contributions for this work is to demonstrate how proteome stoichiometry is regulated across different conditions. A total of m=15 conditions were tested in this study, and this limits the rank of LDA matrix as 14. Therefore, maximally 14 "modes" of differential composition in a proteome can be detected.

As a general reader, I am wondering in the future if one increases or decreases the number of conditions (say m=5 or m=50) what information can be extracted? It is conceivable that increasing different conditions with distinct cellular physiology would be beneficial to "explore" different modes of regulation for cells. As proof of principle, I am wondering if the authors could test a lower number (by sub-sampling from m=15 conditions, e.g. picking five of the most distinct conditions) and see how this would affect the prediction of proteome stoichiometry inference.

We thank the reviewer for bringing an important point to our attention. To address the issue raised, we conducted a new subsampling analysis (Fig. S14).

As we described in the main text (Fig. 6E) and the supplementary materials, the m x m orthogonal matrix, Θ, represents to what extent the two spaces Ω_LE and Ω_B are similar (m is the number of conditions; in our main analysis, m = 15). Thus, the low-dimensional correspondence between the two spaces connected by an orthogonal transformation, such as an m-dimensional rotation, can be evaluated by examining the elements of the matrix Θ. Specifically, large off-diagonal elements of the matrix  mix higher dimensions and lower dimensions, making the two spaces spanned by the first few major axes appear dissimilar. Based on this property, we evaluated the vulnerability of the low-dimensional correspondence between Ω_LE and Ω_B to the reduced number of conditions by measuring how close Θ was to the identity matrix when the analysis was performed on the subsampled datasets.

In the new figure (Fig. S14), we first created all possible smaller condition sets by subsampling the conditions. Next, to evaluate the closeness between the matrix Θ and the identity matrix for each smaller condition set, we generated 10,000 random orthogonal matrices of the same size as . We then evaluated the probability of obtaining a higher level of low-dimensional correspondence than that of the experimental data by chance (see section 1.8 of the Supplementary Materials). This analysis was already performed in the original manuscript for the non-subsampled case (m = 15) in Fig. S9C; the new analysis systematically evaluates the correspondence for the subsampled datasets.

The results clearly show that low-dimensional correspondence is more likely to be obtained with more conditions (Fig. S14). In particular, when the number of conditions used in the analysis exceeds five, the median of the probability that random orthogonal matrices were closer to the identity matrix than the matrix Θ calculated from subsampled experimental data became lower than 10^-4. This analysis provides insight into the number of conditions required to find low-dimensional correspondence between Ω_LE and Ω_B.

What conditions are used in the analysis can change the low-dimensional structures of Ω_LE and Ω_B . Therefore, it is important to clarify whether including more conditions in the analysis reduces the dependence of the low-dimensional structures on conditions. We leave this issue as a subject for future study. This issue relates to the effective dimensionality of omics profiles needed to establish the diverse physiological states of cells across conditions. Determining the minimum number of conditions to attain the condition-independent low-dimensional structures of Ω_LE and Ω_B would provide insight into this fundamental problem. Furthermore, such an analysis would identify the range of applications of Raman spectra as a tool for capturing macroscopic properties of cells at the system level.

We now discuss this point in the Discussion section, referring to this analysis result (Fig. S14). Please also see our reply to the comment (1) by Reviewer #2 (Recommendations for the authors).

(4) In E. coli cells, total proteome is in mM concentration while the total metabolites are between 10 to 100 mM concentration. Since proteins are large molecules with more functional groups, they may contribute to more Raman signal (per molecules) than metabolites. Still, the meaningful quantity here is the "differential Raman signal" with different conditions, not the absolute signal. I am wondering how much percent of differential Raman signature are from proteome and how much are from metabolome.

It is an important and interesting question to what extent changes in the proteome and metabolome contribute to changes in Raman spectra. Though we concluded that answering this question is beyond the scope of this study, we believe it is an important topic for future research.

Raman spectral patterns convey the comprehensive molecular composition spanning the various omics layers of target cells. Changes in the composition of these layers can be highly correlated, and identifying their contributions to changes in Raman spectra would provide insight into the mutual correlation of different omics layers. Addressing the issue raised by the reviewer would expand the applications of Raman spectroscopy and highlight the advantage of cellular Raman spectra as a means of capturing comprehensive multi-omics information.

We note that some studies have evaluated the contributions of proteins, lipids, nucleic acids, and glycogen to the Raman spectra of mammalian cells and how these contributions change in different states (e.g., Mourant et al., J Biomed Opt, 10(3), 031106, 2005). Additionally, numerous studies have imaged or quantified metabolites in various cell types (see, for example, Cutshaw et al., Chemical Reviews, 123(13), 8297–8346, 2023, for a comprehensive review). Extending these approaches to multiple omics layers in future studies would help resolve the issue raised by the reviewer.

(5) It is known that E. coli cells in different conditions have different cell sizes, where cell width increases with carbon source quality and growth rate. Does this effect be normalized when processing the Raman signal?

Each spectrum was normalized by subtracting the average and dividing it by the standard deviation. This normalization minimizes the differences in signal intensities due to different cell sizes and densities. This information is shown in the Materials and Methods section of the Supplementary Materials.

(6) I have a question about interpretation of the centrality index. A higher centrality indicates the protein expression pattern is more aligned with the "mainstream" of the other proteins in the proteome. However, it is possible that the proteome has multiple" mainstream modes" (with possibly different contributions in magnitudes), and the centrality seems to only capture the "primary mode". A small group of proteins could all have low centrality but have very consistent patterns with high conservation of stoichiometry. I wondering if the author could discuss and clarify with this.

We thank the reviewer for drawing our attention to the insufficient explanation in the original manuscript. First, we note that stoichiometry conserving protein groups are not limited to those composed of proteins with high stoichiometry conservation centrality. The SCGs 2–5 are composed of proteins that strongly conserve stoichiometry within each group but have low stoichiometry conservation centrality (Fig. 5A, 5K, 5L, and 7A). In other words, our results demonstrate the existence of the "primary mainstream mode" (SCG 1, i.e., the homeostatic core) and condition-specific "non-primary mainstream modes" (SCGs 2–5). These primary and non-primary modes are distinguishable by their position along the axis of stoichiometry conservation centrality (Fig. 5A, 5K, and 5L).

However, a single one-dimensional axis (centrality) cannot capture all characteristics of stoichiometry-conserving architecture. In our case, the "non-primary mainstream modes" (SCGs 2–5) were distinguished from each other by multiple csLE axes.

To clarify this point, we modified the first paragraph of the section where we first introduce csLE (Revealing global stoichiometry conservation architecture of the proteomes with csLE). We also added a paragraph to the Discussion section regarding the condition-specific SCGs 2–5.

(7) Figures 3, 4, and 5A-I are analyses on proteome data and are not related to Raman spectral data. I am wondering if this part of the analysis can be re-organized and not disrupt the mainline of the manuscript.

We agree that the structure of this manuscript is complicated. Before submitting this manuscript to eLife, we seriously considered reorganizing it. However, we concluded that this structure was most appropriate because our focus on stoichiometry conservation cannot be explained without analyzing the coefficients of the Raman-proteome correspondence using COG classification (see Fig. 3; note that Fig. 3A relates to Raman data). This analysis led us to examine the global stoichiometry conservation architecture of proteomes (Figs. 4 and 5) and discover the unexpected similarity between the low-dimensional structures of Ω_LE and Ω_B

Therefore, we decided to keep the structure of the manuscript as it is. To partially resolve this issue, however, we added references to Fig. S1, the diagram of this paper’s mainline, to several places in the main text so that readers can more easily grasp the flow of the manuscript.

(8) Supplementary Equation (2.6) could be wrong. From my understanding of the coordinate transformation definition here, it should be [w1 ... ws] X := RHS terms in big parenthesis.

We checked the equation and confirmed that it is correct.

Reviewer #2 (Recommendations for the authors):

(1) The first main result or linear map between raman and proteome linked via B is intriguing in the sense that the map is condition-independent. A speculative question I have is if this relationship may become more complex or have more condition-dependent corrections as the number of conditions goes up. The 15 or so conditions are great but it is not clear if they are often quite restrictive. For example, they assume an abundance of most other nutrients. Now if you include a growth rate decrease due to nitrogen or other limitations, do you expect this to work?

In our previous paper (Kobayashi-Kirschvink et al., Cell Systems 7(1): 104–117.e4, 2018), we statistically demonstrated a linear correspondence between cellular Raman spectra and transcriptomes for fission yeast under 10 environmental conditions. These conditions included nutrient-rich and nutrient-limited conditions, such as nitrogen limitation. Since the Raman-transcriptome correspondence was only statistically verified in that study, we analyzed the data from the standpoint of stoichiometry conservation in this study. The results (Fig. S11 and S12) revealed a correspondence in lower dimensions similar to that observed in our main results. In addition, similar correspondences were obtained even for different E. coli strains under common culture conditions (Fig. S11 and S12). Therefore, it is plausible that the stoichiometry-conservation low-dimensional correspondence between Raman and gene expression profiles holds for a wide range of external and internal perturbations.

We agree with the reviewer that it is important to understand how Raman-omics correspondences change with the number of conditions. To address this issue, we examined how the correspondence between Ω_LE and Ω_B changes by subsampling the conditions used in the analysis. We focused on , which was introduced in Fig. 5E, because the closeness of Θ to the identity matrix represents correspondence precision. We found a general trend that the low-dimensional correspondence becomes more precise as the number of conditions increases (Fig. S14). This suggests that increasing the number of conditions generally improves the correspondence rather than disrupting it.

We added a paragraph to the Discussion section addressing this important point. Please also refer to our response to Comment (3) of Reviewer #1 (Recommendations for the authors).

(2) A little more explanation in the text for 3C/D would help. I am imagining 3D is the control for 3C. Minor comment - 3B looks identical to S4F but the y-axis label is different.

We thank the reviewer for pointing out the insufficient explanation of Fig. 3C and 3D in the main text. Following this advice, we added explanations of these plots to the main text. We also added labels ("ISP COG class" and "non-ISP COG class") to the top of these two figures.

Fig. 3B and S4F are different. For simplicity, we used the Pearson correlation coefficient in Fig. 3B. However, cosine similarity is a more appropriate measure for evaluating the degree of conservation of abundance ratios. Thus, we presented the result using cosine similarity in a supplementary figure (Fig. S4F). Please note that each point in Fig. S4F is calculated between proteome vectors of two conditions. The dimension of each proteome vector is the number of genes in each COG class.

(3) Can we see a log-log version of 4C to see how the low-abundant proteins are behaving? In fact, the same is in part true for Figure 3A.

We added the semi-log version of the graph for SCG1 (the homeostatic core) in Fig. 4C to make low-abundant proteins more visible. Please note that the growth rates under the two stationary-phase conditions were zero; therefore, plotting this graph in log-log format is not possible.

Fig. 3A cannot be shown as a log-log plot because many of the coefficients are negative. The insets in the graphs clarify the points near the origin.

(4) In 5L, how should one interpret the other dots that are close to the center but not part of the SCG1? And this theme continues in 6ACD and 7A.

The SCGs were obtained by setting a cosine similarity threshold. Therefore, proteins that are close to SCG 1 (the homeostatic core) but do not belong to it have a cosine similarity below the threshold with any protein in SCG 1. Fig. 7 illustrates the expression patterns of the proteins in question.

(5) Finally, I do not fully appreciate the whole analysis of connecting ¥Omega_csLE and ¥Omega_B and plots in 6 and 7. This corresponds to a lot of linear algebra in the 50 or so pages in section 1.8 in the supplementary. If the authors feel this is crucial in some way it needs to be better motivated and explained. I philosophically appreciate developing more formalism to establish these connections but I did not understand how this (maybe even if in the future) could lead to a new interpretation or analysis or theory.

The mathematical analyses included in the supplementary materials are important for readers who are interested in understanding the mathematics behind our conclusions. However, we also thought these arguments were too detailed for many readers when preparing the original submission and decided to show them in the supplemental materials.

To better explain the motivation behind the mathematical analyses, we revised the section “Representing the proteomes using the Raman LDA axes”.

Please also see our reply to the comment (6) by Reviewer #2 (Recommendations for the authors) below.

(6) Along the lines of the previous point, there seems to be two separate points being made: a) there is a correspondence between Raman and proteins, and b) we can use the protein data to look at centrality, generality, SCGs, etc. And the two don't seem to be linked until the formalism of ¥Omegas?

The reviewer is correct that we can calculate and analyze some of the quantities introduced in this study, such as stoichiometry conservation centrality and expression generality, without Raman data. However, it is difficult to justify introducing these quantities without analyzing the correspondence between the Raman and proteome profiles. Moreover, the definition of expression generality was derived from the analysis of Raman-proteome correspondence (see section 2.2 of the Supplementary Materials). Therefore, point b) cannot stand alone without point a) from its initial introduction.

To partially improve the readability and resolve the issue of complicated structure of this manuscript, we added references to Fig. S1, which is a diagram of the paper’s mainline, to several places in the main text. Please also see our reply to the comment (7) by Reviewer #1 (Recommendations for the authors).

Author response:

We would like to thank the three Reviewers for their thoughtful comments and detailed feedback. We are pleased to hear that the Reviewers found our paper to be “providing more direct evidence for the role of signals in different frequency bands related to predictability and surprise” (R1), “well-suited to test evidence for predictive coding versus alternative hypotheses” (R2), and “timely and interesting” (R3).

We perceive that the reviewers have an overall positive impression of the experiments and analyses, but find the text somewhat dense and would like to see additional statistical rigor, as well as in some cases additional analyses to be included in supplementary material. We therefore here provide a provisional letter addressing revisions we have already performed and outlining the revision we are planning point-by-point. We begin each enumerated point with the Reviewer’s quoted text and our responses to each point are made below.

Reviewer 1:

(1) Introduction:

The authors write in their introduction: "H1 further suggests a role for θ oscillations in prediction error processing as well." Without being fleshed out further, it is unclear what role this would be, or why. Could the authors expand this statement?”

We have edited the text to indicate that theta-band activity has been related to prediction error processing as an empirical observation, and must regrettably leave drawing inferences about its functional role to future work, with experiments designed specifically to draw out theta-band activity.

(2) Limited propagation of gamma band signals:

Some recent work (e.g. https://www.cell.com/cell-reports/fulltext/S2211-1247(23)00503-X) suggests that gamma-band signals reflect mainly entrainment of the fast-spiking interneurons, and don't propagate from V1 to downstream areas. Could the authors connect their findings to these emerging findings, suggesting no role in gamma-band activity in communication outside of the cortical column?”

We have not specifically claimed that gamma propagates between columns/areas in our recordings, only that it synchronizes synaptic current flows between laminar layers within a column/area. We nonetheless suggest that gamma can locally synchronize a column, and potentially local columns within an area via entrainment of local recurrent spiking, to update an internal prediction/representation upon onset of a prediction error. We also point the Reviewer to our Discussion section, where we state that our results fit with a model “whereby θ oscillations synchronize distant areas, enabling them to exchange relevant signals during cognitive processing.” In our present work, we therefore remain agnostic about whether theta or gamma or both (or alternative mechanisms) are at play in terms of how prediction error signals are transmitted between areas.

(3) Paradigm:

While I agree that the paradigm tests whether a specific type of temporal prediction can be formed, it is not a type of prediction that one would easily observe in mice, or even humans. The regularity that must be learned, in order to be able to see a reflection of predictability, integrates over 4 stimuli, each shown for 500 ms with a 500 ms blank in between (and a 1000 ms interval separating the 4th stimulus from the 1st stimulus of the next sequence). In other words, the mouse must keep in working memory three stimuli, which partly occurred more than a second ago, in order to correctly predict the fourth stimulus (and signal a 1000 ms interval as evidence for starting a new sequence).

A problem with this paradigm is that positive findings are easier to interpret than negative findings. If mice do not show a modulation to the global oddball, is it because "predictive coding" is the wrong hypothesis, or simply because the authors generated a design that operates outside of the boundary conditions of the theory? I think the latter is more plausible. Even in more complex animals, (eg monkeys or humans), I suspect that participants would have trouble picking up this regularity and sequence, unless it is directly task-relevant (which it is not, in the current setting). Previous experiments often used simple pairs (where transitional probability was varied, eg, Meyer and Olson, PNAS 2012) of stimuli that were presented within an intervening blank period. Clearly, these regularities would be a lot simpler to learn than the highly complex and temporally spread-out regularity used here, facilitating the interpretation of negative findings (especially in early cortical areas, which are known to have relatively small temporal receptive fields).

I am, of course, not asking the authors to redesign their study. I would like to ask them to discuss this caveat more clearly, in the Introduction and Discussion, and situate their design in the broader literature. For example, Jeff Gavornik has used much more rapid stimulus designs and observed clear modulations of spiking activity in early visual regions. I realize that this caveat may be more relevant for the spiking paper (which does not show any spiking activity modulation in V1 by global predictability) than for the current paper, but I still think it is an important general caveat to point out.”

We appreciate the Reviewer’s concern about working memory limitations in mice. Our paradigm and training followed on from previous paradigms such as Gavornik and Bear (2014), in which predictive effects were observed in mouse V1 with presentation times of 150ms and interstimulus intervals of 1500ms. In addition, we note that Jamali et al. (2024) recently utilized a similar global/local paradigm in the auditory domain with inter-sequence intervals as long as 28-30 seconds, and still observed effects of a predicted sequence (https://elifesciences.org/articles/102702). For the revised manuscript, we plan to expand on this in the Discussion section.

That being said, as the Reviewer also pointed out, this would be a greater concern had we not found any positive findings in our study. However, even with the rather long sequence periods we used, we did find positive evidence for predictive effects, supporting the use of our current paradigm. We agree with the reviewer that these positive effects are easier to interpret than negative effects, and plan to expand upon this in the Discussion when we resubmit.

(4) Reporting of results:

I did not see any quantification of the strength of evidence of any of the results, beyond a general statement that all reported results pass significance at an alpha=0.01 threshold. It would be informative to know, for all reported results, what exactly the p-value of the significant cluster is; as well as for which performed tests there was no significant difference.”

For the revised manuscript, we can include the p-values after cluster-based testing for each significant cluster, as well as show data that passes a more stringent threshold of p<0.001 (1/1000) or p<0.005 (1/200) rather than our present p<0.01 (1/100).

(5) Cluster test:

The authors use a three-dimensional cluster test, clustering across time, frequency, and location/channel. I am wondering how meaningful this analytical approach is. For example, there could be clusters that show an early difference at some location in low frequencies, and then a later difference in a different frequency band at another (adjacent) location. It seems a priori illogical to me to want to cluster across all these dimensions together, given that this kind of clustering does not appear neurophysiologically implausible/not meaningful. Can the authors motivate their choice of three-dimensional clustering, or better, facilitating interpretability, cluster eg at space and time within specific frequency bands (2d clustering)?”

We are happy to include a 3D plot of a time-channel-frequency cluster in the revised manuscript to clarify our statistical approach for the reviewer. We consider our current three-dimensional cluster-testing an “unsupervised” way of uncovering significant contrasts with no theory-driven assumptions about which bounded frequency bands or layers do what.

Reviewer 2:

Sennesh and colleagues analyzed LFP data from 6 regions of rodents while they were habituated to a stimulus sequence containing a local oddball (xxxy) and later exposed to either the same (xxxY) or a deviant global oddball (xxxX). Subsequently, they were exposed to a controlled random sequence (XXXY) or a controlled deterministic sequence (xxxx or yyyy). From these, the authors looked for differences in spectral properties (both oscillatory and aperiodic) between three contrasts (only for the last stimulus of the sequence).

(1) Deviance detection: unpredictable random (XXXY) versus predictable habituation (xxxy)

(2) Global oddball: unpredictable global oddball (xxxX) versus predictable deterministic (xxxx), and

(3) "Stimulus-specific adaptation:" locally unpredictable oddball (xxxY) versus predictable deterministic (yyyy).

They found evidence for an increase in gamma (and theta in some cases) for unpredictable versus predictable stimuli, and a reduction in alpha/beta, which they consider evidence towards the "predictive routing" scheme.

While the dataset and analyses are well-suited to test evidence for predictive coding versus alternative hypotheses, I felt that the formulation was ambiguous, and the results were not very clear. My major concerns are as follows:”

We appreciate the reviewer’s concerns and outline how we will address them below:

(1) The authors set up three competing hypotheses, in which H1 and H2 make directly opposite predictions. However, it must be noted that H2 is proposed for spatial prediction, where the predictability is computed from the part of the image outside the RF. This is different from the temporal prediction that is tested here. Evidence in favor of H2 is readily observed when large gratings are presented, for which there is substantially more gamma than in small images. Actually, there are multiple features in the spectral domain that should not be conflated, namely (i) the transient broadband response, which includes all frequencies, (ii) contribution from the evoked response (ERP), which is often in frequencies below 30 Hz, (iii) narrow-band gamma oscillations which are produced by large and continuous stimuli (which happen to be highly predictive), and (iv) sustained low-frequency rhythms in theta and alpha/beta bands which are prominent before stimulus onset and reduce after ~200 ms of stimulus onset. The authors should be careful to incorporate these in their formulation of PC, and in particular should not conflate narrow-band and broadband gamma.”

We have clarified in the manuscript that while the gamma-as-prediction hypothesis (our H2) was originally proposed in a spatial prediction domain, further work (specifically Singer (2021)) has extended the hypothesis to cover temporal-domain predictions as well.

To address the reviewer’s point about multiple features in the spectral domain: Our analysis has specifically separated aperiodic components using FOOOF analysis (Supp. Fig. 1) and explicitly fit and tested aperiodic vs. periodic components (Supp. Figs 1&2). We did not find strong effects in the aperiodic components but did in the periodic components (Supp. Fig. 2), allowing us to be more confident in our conclusions in terms of genuine narrow-band oscillations. In the revised manuscript, we will include analysis of the pre-stimulus time window to address the reviewer’s point (iv) on sustained low frequency oscillations.

(2) My understanding is that any aspect of predictive coding must be present before the onset of stimulus (expected or unexpected). So, I was surprised to see that the authors have shown the results only after stimulus onset. For all figures, the authors should show results from -500 ms to 500 ms instead of zero to 500 ms.

In our revised manuscript we will include a pre-stimulus analysis and supplementary figures with time ranges from -500ms to 500ms. We have only refrained from doing so in the initial manuscript because our paradigm’s short interstimulus interval makes it difficult to interpret whether activity in the ISI reflects post-stimulus dynamics or pre-stimulus prediction. Nonetheless, we can easily show that in our paradigm, alpha/beta-band activity is elevated in the interstimulus activity after the offset of the previous stimulus, assuming that we baseline to the pre-trial period.

(3) In many cases, some change is observed in the initial ~100 ms of stimulus onset, especially for the alpha/beta and theta ranges. However, the evoked response contributes substantially in the transient period in these frequencies, and this evoked response could be different for different conditions. The authors should show the evoked responses to confirm the same, and if the claim really is that predictions are carried by genuine "oscillatory" activity, show the results after removing the ERP (as they had done for the CSD analysis).

We have included an extra sentence in our Materials and Methods section clarifying that the evoked potential/ERP was removed in our existing analyses, prior to performing the spectral decomposition of the LFP signal. We also note that the FOOOF analysis we applied separates aperiodic components of the spectral signal from the strictly oscillatory ones.

In our revised manuscript we will include an analysis of the evoked responses as suggested by the reviewer.

(4) I was surprised by the statistics used in the plots. Anything that is even slightly positive or negative is turning out to be significant. Perhaps the authors could use a more stringent criterion for multiple comparisons?

As noted above to Reviewer 1 (point 4), we are happy to include supplemental figures in our resubmission showing the effects on our results of setting the statistical significance threshold with considerably greater stringency.

(5) Since the design is blocked, there might be changes in global arousal levels. This is particularly important because the more predictive stimuli in the controlled deterministic stimuli were presented towards the end of the session, when the animal is likely less motivated. One idea to check for this is to do the analysis on the 3rd stimulus instead of the 4th? Any general effect of arousal/attention will be reflected in this stimulus.

In order to check for the brain-wide effects of arousal, we plan to perform similar analyses to our existing ones on the 3rd stimulus in each block, rather than just the 4th “oddball” stimulus. Clusters that appear significantly contrasting in both the 3rd and 4th stimuli may be attributable to arousal.  We will also analyze pupil size as an index of arousal to check for arousal differences between conditions in our contrasts, possibly stratifying our data before performing comparisons to equalize pupil size within contrasts. We plan to include these analyses in our resubmission.

(6) The authors should also acknowledge/discuss that typical stimulus presentation/attention modulation involves both (i) an increase in broadband power early on and (ii) a reduction in low-frequency alpha/beta power. This could be just a sensory response, without having a role in sending prediction signals per se. So the predictive routing hypothesis should involve testing for signatures of prediction while ruling out other confounds related to stimulus/cognition. It is, of course, very difficult to do so, but at the same time, simply showing a reduction in low-frequency power coupled with an increase in high-frequency power is not sufficient to prove PR.

Since many different predictive coding and predictive processing hypotheses make very different hypotheses about how predictions might encoded in neurophysiological recordings, we have focused on prediction error encoding in this paper.

For the hypothesis space we have considered (H1-H3), each hypothesis makes clearly distinguishable predictions about the spectral response during the time period in the task when prediction errors should be present. As noted by the reviewer, a transient increase in broadband frequencies would be a signature of H3. Changes to oscillatory power in the gamma band in distinct directions (e.g., increasing or decreasing with prediction error) would support either H1 and H2, depending on the direction of change. We believe our data, especially our use of FOOOF analysis and separation of periodic from aperiodic components, coupled to the three experimental contrasts, speaks clearly in favor of the Predictive Routing model, but we do not claim we have “proved” it. This study provides just one datapoint, and we will acknowledge this in our revised Discussion in our resubmission.

(7) The CSD results need to be explained better - you should explain on what basis they are being called feedforward/feedback. Was LFP taken from Layer 4 LFP (as was done by van Kerkoerle et al, 2014)? The nice ">" and "<" CSD patterns (Figure 3B and 3F of their paper) in that paper are barely observed in this case, especially for the alpha/beta range.

We consider a feedforward pattern as flowing from L4 outwards to L2/3 and L5/6, and a feedback pattern as flowing in the opposite direction, from L1 and L6 to the middle layers. We will clarify this in the revised manuscript.

Since gamma-band oscillations are strongest in L2/3, we re-epoched LFPs to the oscillation troughs in L2/3 in the initial manuscript. We can include in the revised manuscript equivalent plots after finding oscillation troughs in L4 instead, as well as calculating the difference in trough times within-band between layers to quantify the transmission delay and add additional rigor to our feedforward vs. feedback interpretation of the CSD data.

(8) Figure 4a-c, I don't see a reduction in the broadband signal in a compared to b in the initial segment. Maybe change the clim to make this clearer?

We are looking into the clim/colorbar and plot-generation code to figure out the visibility issue that the Reviewer has kindly pointed out to us.

(9) Figure 5 - please show the same for all three frequency ranges, show all bars (including the non-significant ones), and indicate the significance (p-values or by *, **, ***, etc) as done usually for bar plots.

We will add the requested bar-plots for all frequency ranges, though we note that the bars given here are the results of adding up the spectral power in the channel-time-frequency clusters that already passed significance tests and that adding secondary significance tests here may not prove informative.

(10) Their claim of alpha/beta oscillations being suppressed for unpredictable conditions is not as evident. A figure akin to Figure 5 would be helpful to see if this assertion holds.

As noted above, we will include the requested bar plot, as well as examining alpha/beta in the pre-stimulus time-series rather than after the onset of the oddball stimulus.

(11) To investigate the prediction and violation or confirmation of expectation, it would help to look at both the baseline and stimulus periods in the analyses.

We will include for the Reviewer’s edification a supplementary figure showing the spectrograms for the baseline and full-trial periods to look at the difference between baseline and prestimulus expectation.

Reviewer 3:

Summary:

In their manuscript entitled "Ubiquitous predictive processing in the spectral domain of sensory cortex", Sennesh and colleagues perform spectral analysis across multiple layers and areas in the visual system of mice. Their results are timely and interesting as they provide a complement to a study from the same lab focussed on firing rates, instead of oscillations. Together, the present study argues for a hypothesis called predictive routing, which argues that non-predictable stimuli are gated by Gamma oscillations, while alpha/beta oscillations are related to predictions.

Strengths:

(1) The study contains a clear introduction, which provides a clear contrast between a number of relevant theories in the field, including their hypotheses in relation to the present data set.

(2) The study provides a systematic analysis across multiple areas and layers of the visual cortex.”

We thank the Reviewer for their kind comments.

Weaknesses:

(1) It is claimed in the abstract that the present study supports predictive routing over predictive coding; however, this claim is nowhere in the manuscript directly substantiated. Not even the differences are clearly laid out, much less tested explicitly. While this might be obvious to the authors, it remains completely opaque to the reader, e.g., as it is also not part of the different hypotheses addressed. I guess this result is meant in contrast to reference 17, by some of the same authors, which argues against predictive coding, while the present work finds differences in the results, which they relate to spectral vs firing rate analysis (although without direct comparison).

We agree that in this manuscript we should restrict ourselves to the hypotheses that were directly tested. We have revised our abstract accordingly,  and softened our claim to note only that our LFP results are compatible with predictive routing.

(2) Most of the claims about a direction of propagation of certain frequency-related activities (made in the context of Figures 2-4) are - to the eyes of the reviewer - not supported by actual analysis but glimpsed from the pictures, sometimes, with very little evidence/very small time differences to go on. To keep these claims, proper statistical testing should be performed.

In our revised manuscript, we will either substantiate (with quantification of CSD delays between layers) or soften the claims about feedforward/feedback direction of flow within the cortical column.

(3) Results from different areas are barely presented. While I can see that presenting them in the same format as Figures 2-4 would be quite lengthy, it might be a good idea to contrast the right columns (difference plots) across areas, rather than just the overall averages.

In our revised manuscript we will gladly include a supplementary figure showing the right-column difference plots across areas, in order to make sure to include aspects of our dataset that span up and down the cortical hierarchy.

(4) Statistical testing is treated very generally, which can help to improve the readability of the text; however, in the present case, this is a bit extreme, with even obvious tests not reported or not even performed (in particular in Figure 5).

We appreciate the Reviewer’s concern for statistical rigor, and as noted to the other reviewers, we can add different levels of statistical description and describe the p-values associated with specific clusters. Regarding Figure 5, we must protest as the bar heights were computed came from clusters already subjected to statistical testing and found significant.  We could add a supplementary figure which considers untested narrowband activity and tests it only in the “bar height” domain, if the Reviewer would like.

(5) The description of the analysis in the methods is rather short and, to my eye, was missing one of the key descriptions, i.e., how the CSD plots were baselined (which was hinted at in the results, but, as far as I know, not clearly described in the analysis methods). Maybe the authors could section the methods more to point out where this is discussed.

We have added some elaboration to our Materials and Methods section, especially to specify that CSD, having physical rather than arbitrary units, does not require baselining.

(6) While I appreciate the efforts of the authors to formulate their hypotheses and test them clearly, the text is quite dense at times. Partly this is due to the compared conditions in this paradigm; however, it would help a lot to show a visualization of what is being compared in Figures 2-4, rather than just showing the results.

In the revised manuscript we will add a visual aid for the three contrasts we consider.

We are happy to inform the editors that we have implemented, for the Reviewed Preprint, the direct textual Recommendations for the Authors given by Reviewers 2 and 3. We will implement the suggested Figure changes in our revised manuscript. We thank them for their feedback in strengthening our manuscript.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

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.

We thank the reviewer for their kind comments and clear summary of the paper and its strengths.

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.

We agree with the reviewer and have added a schematic figure of the method (figure 1a).

(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.

We thank the reviewer for their comments. We agree that the null result regarding the community structures does not mean that EC doesn’t generalise over these structures, and that the training order could in theory contribute to the lack of an effect. The decision to keep the asymmetry of the training order was deliberate: we chose this order based on our previous study (Mark et al. 2020), where we show that learning a community structure first changes the learning strategy of subsequent graphs. We could have perhaps overcome this by increasing the training periods, but 1) the training period is already very long; 2) there will still be asymmetry because the group that first learn community structure will struggle in learning the hexagonal graph more than vice versa, as shown in Mark et al. 2020.

We have added the following sentences on this decision to the Methods section:

“We chose to first teach hexagonal graphs for all participants and not randomize the order because of previous results showing that first learning community structure changes participants’ learning strategy (mark et al. 2020).”

(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).

Thanks for this suggestion. We indeed tried to run the analysis in a whole-ROI approach, but this did not result in a significant effect in EC. Importantly, we disagree with the reviewer that this is a “better way to show specificity” than the searchlight approach. In our view, the two analyses differ with respect to the spatial extent of the representation they test for. The searchlight approach is testing for a highly localised representation on the scale of small spheres with only 100 voxels. The signal of such a localised representation is likely to be drowned in the noise in an analysis that includes thousands of voxels which mostly don’t show the effect - as would be the case in the whole-ROI approach.

(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.

See our response to comment (2).

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.

We thank the reviewer for their kind comments and the clear summary of our paper.

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.

We thank the reviewer for the comment. We agree that the paper comes across as a bit of a methods-empirical hybrid. We chose to do this because we believe (as the reviewer also points out) that there is value in both aspects of the paper.

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.

We thank the reviewer for their comments. We would like to point out that we demean each voxel within all states/piles (3-pictures sequences) in a given graph/task (what the reviewer is calling “a condition”). Hence there is no shared univariate activation of many voxels in response to a graph going into the computation, and no sensitivity to the overall firing rate/voxel activation.  Our calculation captures the variance across states conditions within a task (here a graph), over and above the univariate effect of graph activity. In addition, we spatially pre-whiten the data within each searchlight, meaning that noisy voxels with high noise variance will be downweighted and noise correlations between voxels are removed prior to applying our method.

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?

We thank the reviewer for this important and interesting point. We agree that calculating correlation between the upper triangular elements of the covariance or correlation matrices picks up similar, but not identical aspects of the data (see below the mathematical explanation that was added to the supplementary). When we repeated the searchlight analysis and calculated the correlation between the upper triangular entries of the Pearson correlation matrices we obtained an effect in the EC, though weaker than with our subspace generalization method (t=3.9, the effect did not survive multiple comparisons). Similar results were obtained with the correlation between the upper triangular elements of the covariance matrices(t=3.8, the effect did not survive multiple comparisons).

The difference between the two methods is twofold: 1) Our method is based on the covariance matrix and not the correlation matrix - i.e. a difference in normalisation. We realised that in the main text of the original paper we mistakenly wrote “correlation matrix” rather than “covariance matrix” (though our equations did correctly show the covariance matrix). We have corrected this mistake in the revised manuscript. 2) The weighting of the variance explained in the direction of each eigenvector is different between the methods, with some benefits of our method for identifying low-dimensional representations and for robustness to strong spatial correlations.  We have added a section “Subspace Generalisation vs correlating the Neuron-by-Neuron correlation matrices” to the supplementary information with a mathematical explanation of these differences.

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?

This is a searchlight analysis, therefore it captures the activity patterns within nearby voxels. Indeed, as we show in our simulation, areas with high activity and therefore high signal to noise will have better signal in our method as well. Note that this is true of most measures.

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.

We agree with this point, yet believe that the results still shed light on EC functionality. Unfortunately, we could not find correlation between behavioral measures and the fMRI effect.

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.

We thank the reviewer for their comments. We agree with the reviewer that this is a very interesting question. We tried to look for effects in the mPFC, but we did not obtain results that were strong enough to report in the main manuscript, but we do report a small effect in the supplementary.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) I wonder how important the PCA on B1(voxel-by-state matrix from environment 1) and the computation of the AUC (from the projection on B2 [voxel-by-state matrix from environment 1]) is for the analysis to work. Would you not get the same result if you correlated the voxel-by-voxel correlation matrix based on B1 (C1) with the voxel-by-voxel correlation matrix based on B2 (C2)? I understand that you would not have the subspace-by-subspace resolution that comes from the individual eigenvectors, but would the AUC not strongly correlate with the correlation between C1 and C2?

We agree with the reviewer comments - see our response to reviewer 2 second issue above. 

(2) There is a subtle difference between how the method is described for the neural recording and fMRI data. Line 695 states that principal components of the neuron x neuron intercorrelation matrix are computed, whereas line 888 implies that principal components of the data matrix B are computed. Of note, B is a voxel x pile rather than a pile x voxel matrix. Wouldn't this result in U being pile x pile rather than voxel x voxel?

The PCs are calculated on the neuron x neuron (or voxel x voxel) covariance matrix of the activation matrix. We’ve added the following clarification to the relevant part of the Methods:

“We calculated noise normalized GLM betas within each searchlight using the RSA toolbox. For each searchlight and each graph, we had a nVoxels (100) by nPiles (10) activation matrix (B) that describes the activation of a voxel as a result of a particular pile (three pictures’ sequence). We exploited the (voxel x voxel) covariance matrix of this matrix to quantify the manifold alignment within each searchlight.”

(3) It would be very helpful to the field if the authors would make the code and data publicly available. Please consider depositing the code for data analysis and simulations, as well as the preprocessed/extracted data for the key results (rat data/fMRI ROI data) into a publicly accessible repository.

The code is publicly available in git (https://github.com/ShirleyMgit/subspace_generalization_paper_code/tree/main).

(4) Line 219: "Kolmogorov Simonov test" should be "Kolmogorov Smirnov test".

thanks!

(5) Please put plots in Figure 3F on the same y-axis.

(6) Were large and small graphs of a given statistical structure learned on the same days, and if so, sequentially or simultaneously? This could be clarified.

The graphs are learned on the same day.  We clarified this in the Methods section.

Reviewer #2 (Recommendations for the authors):

Perhaps the advantage of the method described here is that you could narrow things down to the specific eigenvector that is doing the heavy lifting in terms of generalization... and then you could look at that eigenvector to see what aspect of the covariance structure persists across conditions of interest. For example, is it just the highest eigenvalue eigenvector that is likely picking up on correlations across the entire neural population? Or is there something more specific going on? One could start to get at this by looking at Figures 1A and 1C - for example, the primary difference for within/between condition generalization in 1C seems to emerge with the first component, and not much changes after that, perhaps suggesting that in this case, the analysis may be picking up on something like the overall level of correlations within different conditions, rather than a more specific pattern of correlations.

The nature of the analysis means the eigenvectors are organized by their contribution to the variance, therefore the first eigenvector is responsible for more variance than the other, we did not check rigorously whether the variance is then splitted equally by the remaining eigenvectors but it does not seems to be the case.

Why is variance explained above zero for fraction EVs = 0 for figure 1C (but not 1A) ? Is there some plotting convention that I'm missing here?

There was a small bug in this plot and it was corrected - thank you very much!

The authors say:

"Interestingly, the difference in AUCs was also 190 significantly smaller than chance for place cells (Figure 1a, compare dotted and solid green 191 lines, p<0.05 using permutation tests, see statistics and further examples in supplementary 192 material Figure S2), consistent with recent models predicting hippocampal remapping that is 193 not fully random (Whittington et al. 2020)."

But my read of the Whittington model is that it would predict slight positive relationships here, rather than the observed negative ones, akin to what one would expect if hippocampal neurons reflect a nonlinear summation of a broad swath of entorhinal inputs.

Smaller differences than chance imply that the remapping of place cells is not completely random.

Figure 2:

I didn't see any description of where noise amplitude values came from - or any justification at all in that section. Clearly, the amount of noise will be critical for putting limits on what can and cannot be detected with the method - I think this is worthy of characterization and explanation. In general, more information about the simulations is necessary to understand what was done in the pseudovoxel simulations. I get the gist of what was done, but these methods should clear enough that someone could repeat them, and they currently are not.

Thanks, we added noise amplitude to the figure legend and Methods.

What does flexible mean in the title? The analysis only worked for the hexagonal grid - doesn't that suggest that whatever representations are uncovered here are not flexible in the sense of being able to encode different things?

Flexible here means, flexible over stimulus’ characteristics that are not related to the structural form such as stimuli, the size of the graph etc.

Reviewer #3 (Recommendations for the authors):

I have noticed that the authors have updated the previous preprint version to include extensive simulations. I believe this addition helps address potential criticisms regarding the signal-to-noise ratio. If the authors could share the code for the fMRI data and the simulations in an open repository, it would enhance the study's impact by reaching a broader readership across various research fields. Except for that, I have nothing to ask for revision.

Thanks, the code will be publicly available: (https://github.com/ShirleyMgit/subspace_generalization_paper_code/tree/main).

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Manuscript number: RC-2025-03160

Corresponding author(s) Padinjat, Raghu

[The “revision plan” should delineate the revisions that authors intend to carry out in response to the points raised by the referees. It also provides the authors with the opportunity to explain their view of the paper and of the referee reports.

• *

The document is important for the editors of affiliate journals when they make a first decision on the transferred manuscript. It will also be useful to readers of the reprint and help them to obtain a balanced view of the paper.

• *

If you wish to submit a full revision, please use our "Full Revision" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

1. General Statements [optional]

We thank all three reviewers for appreciating the novelty of our analysis of CERT function in a physiological context in vivo. While many studies have been published on the biochemistry and function of CERT in cultured cells, there are limited studies, if any, relating the impact of CRT function at the biochemical level to its function on a physiological process, in our case the electrical response to light.

We also that all reviewers for commenting on the importance of our rescue of dcert mutants with hCERT and the scientific insights raised by this experiment. All reviewers have also noted the importance of strengthening our observation that hCERT, in these cells, is localized at ER-PM MCS rather that the more widely reported localization at the Golgi. We highlight that many excellent studies which have localized CERT at the Golgi are performed in cultured, immortalized, mammalian cells. There are limited studies on the localization of this protein in primary cells, neurons or in polarized cells. With the additional experiments we have proposed in the revision for this aspect of the manuscript, we believe the findings will be of great novelty and widespread interest.

We believe we can address almost all points raised by reviewers thereby strengthening this exciting manuscript.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

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

This manuscript dissects the physiological function of ceramide transfer protein (CERT) by studying the phenotype of CERT null Drosophila.

dCERT null animals have a reduced electrical response to light in their photoreceptors, reduced baseline PIP2 accumulation in the cells and delayed re-synthesis of PIP2 and its precursor, PI4P after light stimulation. There are also reduced ER:PM contact sites at the rhabdomere and a corresponding reduction in the localization of PI/PA exchange protein, RDGB at this site. Therefore, the animals seem to have an impaired ability for sustaining phototransduction, which is nonetheless milder than that seen after loss of RDGB, for example. In terms of biochemical function, there is no overall change in ceramides, with some minor increases in specific short chain pools. There is however a large decrease in PE-ceramide species, again selective for a few molecular species. Curiously, decreasing ceramides with a mutant in ceramide synthesis is able to partially rescue both the electrical response and RDGB localization in dCERT flies, implying the increased ceramide species contribute to the phenotype. In addition, a mutation in PE-ceramide synthase largely phenocopies the dCERT null, exhiniting both increases ceramides and decreased PE-ceramide.

In addition, dCERT flies were shown to have reduced localization of some plasma membrane proteins to detergent-resistant membrane fractions, as well as up regulation of the IRE1 and PERK stress-response pathways. Finally, dCERT nulls could be rescued with the human CERT protein, demonstrating conservation of core physiological function between these animals. Surprisingly, CERT is reported to localize to the ER:PM junctions at rhabdomeres, as opposed to the expected ER:Golgi contact sites. Specific areas where the manuscript could be strengthened include:

Figure 2 studies the phototransduction system. Although clear changes in PI4P and PIP2 are seen, it would be interesting to see if changed PA accumulation occur in the dCERT animals, since RDGB localization is disrupted: this is expected to cause PM PA accumulation along with reduced PIP2 synthesis.

It is an important question raised by the reviewer to check PA levels. In the present study we have noticed that localization of RDGB at the base of the rhabdomere in dcert1 is reduced but not completely removed. Consequently, one may consider the situation on dcert1 as a partial loss of function of RDGB and consistent with this, the delay in PI4P and PI(4,5)P2 resynthesis is not as severe as in rdgB9 which is a strong hypomorph (PMID: 26203165).

rdgB9 mutants also show an elevation in PA levels and the reviewer is right that one might expect changes in PA levels too as RDGB is a PI/PA transfer protein. We expect that if measured, there will be a modest elevation in PA levels. However, previous work has shown that elevation of PA levels at the or close to the rhabdomere lead to retinal degeneration Specifically, elevated PA levels by dPLD overexpression disrupts rhabdomere biogenesis and leads to retinal degeneration (PMID: 19349583). Similarly, loss of the lipid transfer protein RDGB leads to photoreceptor degeneration (PMID: 26203165). In this study, we report that retinal degeneration is not a phenotype of dcert1. Thus measurements of PA levels though interesting may not be that informative in the context of the present study. However, if necessary, we can measure PA levels in dcert1.

Lines 228-230 state: "These findings suggest an important contribution for reduced PE - Cer levels in the eye phenotypes of dcert". Does it not also suggest a contribution of the elevated ceramide species, since these are also observed in the CPES animals?

We agree with the reviewer that not only reduced PE-Ceramide but also elevated ceramide levels in GMR>CPESi could contribute to the eye phenotype. This statement will be revised to reflect this conclusion.

Figure 6D is a key finding that human CERT localized to the rhabdomere at ER:PM contact sites, though the reviewer was not convinced by these images. Is the protein truly localized to the contact sites, or simply have a pool of over-expressed protein localized to the surrounding cytoplasm? It also does not rule out localization (and therefore function) at ER:PM contact sites.

Since hCERT completely rescued eye phenotype of dcert1 the localization we observe for hCERT must be at least partly relevant. We will perform additional IHC experiments to

• Co-localize hCERT with an ER-PM MCS marker, e.g RDGB in wild type flies
• Co-localize hCERT with VAP-A that is enriched at the ER-PM MCS. This should help to determine if there are MCS and non-MCS pools of hCERT in these cells. marker, e.g RDGB in wild type flies
• Test if there is a pool of hCERT, in these cells that also localizes (or not) with the Golgi marker Golgin 84. These will be included in the revision to strengthen this important point.

Statistics: There are a large number of t-tests employed that do not correct for multiple comparisons, for example in figures 3B, 3D, 3H, 4C, 6C, S2A, S2B, S3B and S3C.

We will performed multiple comparisons with mentioned data and incorporate in the revised manuscript.

There are two Western blotting sections in the methods.

The first Western blotting methods is for general blots in the paper. The second western blotting section is related to the samples from detergent resistant membrane (DRM) fractions. We will clearly explain this information in the methods section of the manuscript.

Reviewer #1 (Significance (Required)):

Overall, the manuscript is clearly and succinctly written, with the data well presented and mostly convincing. The paper demonstrates clear phenotypes associated with loss of dCERT function, with surprising consequences for the function of a signaling system localized to ER:PM contact sites. To this reviewer, there seem to be three cogent observations of the paper: (i) loss of dCERT leads to accumulation of ceramides and loss of PE-ceramide, which together drive the phenotype. (ii) this ceramide alteration disrupts ER:PM contact sites and thus impairs phototransduction and (iii) rescue by human CERT and its apparent localization to ER:PM contact sites implies a potential novel site of action. Although surprising and novel, the significance of these observations are a little unclear: there is no obvious mechanism by which the elevated ceramide species and decreased PE-ceramide causes the specific failure in phototrasnduction, and the evidence for a novel site of action of CERT at the ER:PM contact sites is not compelling. Therefore, although an interesting and novel set of observations, the manuscript does not reveal a clear mechanistic basis for CERT physiological function.

We thank reviewer for appreciating the quality of our manuscript while also highlighting points through which its impact can be enhanced. To our knowledge this is one of the first studies to tackle the challenging problem of a role for CERT in physiological function. We would like to highlight two points raised:

• We do understand that the localisation of hCERT at ER-PM MCS is unusual compared to the traditional reported localization to ER-Golgi sites. This is important for the overall interpretation of the results in the paper on how dCERT regulates phototransduction. As indicated in response to an earlier comment by the reviewer we will perform additional experiments to strengthen our conclusion of the localization of hCERT.
• With regard to how loss of dCERT affects phototransduction, we feel to likely mechanisms contribute. If the localization of hCERT to ER-PM MCS is verified through additional experiments (see proposal above) then it is important to note that ER-PM MCS in these cells includes the SMC (smooth endoplasmic reticulum) the major site of lipid synthesis. It is possible that loss of dCERT leads to ceramide accumulation in the smooth ER and disruption of ER-PM contacts. That may explain why reducing the levels of ceramide at this site partially rescues the eye phenotype.

The multi-protein INAD-TRP-NORPA complex, central to phototransduction have previously been shown to localise to DRMs in photoreceptors. PE-Ceramides are important contributors to the formation of plasma membrane DRMs and we have presented biochemical evidence that the formation of these DRMs are reduced in the dcert1. This may be a mechanism contributing to reduced phototransduction. This latter mechanism has been proposed as a physiological function of DRMs but we think our data may be the first to show it in a physiological model.

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

Summary Non-vesicular lipid transfer by lipid transfer proteins regulates organelle lipid compositions and functions. CERT transfers ceramide from the ER to Golgi to produce sphingomyelin, although CERT function in animal development and physiology is less clear. Using dcert1 (a protein-null allele), this paper shows a disruption of the sole Drosophila CERT gene causes reduced ERG amplitude in photoreceptors. While the level and localization of phototransduction machinery appears unaffected, the level of PIP2 and the localization of RDGB are perturbed. Collectively, these observations establish a novel link between CERT and phospholipase signaling in phototransduction. To understand the molecular mechanism further, the authors performed lipid chromatography and mass spec to characterize ceramide species in dcert1. This analysis reveals that whereas the total ceramide remains unaffected, most PE-ceramide species are reduced. The authors use lace mutant (serine palmitoyl transferase) and CPES (ceramide phosphoethanolamine synthase) RNAi to distinguish whether it is the accumulation of ceramide in the ER or the reduction of sphingolipid derivates in the Golgi that is the cause for the reduced ERG amplitude. Mutating one copy of lace reduces ceramide level by 50% and partially rescues the ERG defect, suggesting that the accumulation of ceramide in the ER is a cause. CPES RNAi phenocopies the reduced ERG amplitude, suggesting the production of certain sphingolipid is also relevant.

Major comments: 1. By showing the reduced PIP2 level, the decreased SMC sites at the base of rhabdomeres, and the diffused RDGB localization in dcert1, the authors favor the model, in which the disruption of ceramide metabolism affects PIP transport. However, it is unclear if the reduced PIP2 level (i.e., reduced PH-PLCd::GFP staining) is specific to the rhabdomeres. It should be possible to compare PH-PLCd::GFP signals in different plasma membranes between wildtype and dcert1. If PH-PLCd::GFP signal is specifically reduced at the rhabdomeres, this conclusion will be greatly strengthened. In addition, the photoreceptor apical plasma membrane includes rhabdomere and stalk membrane. Is the PH-PLCd::GFP signal at the stalk membrane also affected?

Due to the physical organization of optics in the fly eye, the pseudopupil imaging method used in this study collects the signal for the PIP2 probe (PH-PLCd::GFP) mainly from the apical rhabdomere membrane of photoreceptors in live imaging experimental mode. Therefore, the PIP2 signal from these experiments cannot be used to interpret the level of PIP2 either at the stalk membrane or indeed the basolateral membrane.

The point raised by the reviewer, i.e whether CERT selectively controls PIP2 levels at the rhabdomere membrane or not, is an interesting one. To do this, we will need to fix fly photoreceptors and determine the PH-PLCd::GFP signal using single slice confocal imaging. When combined with a stalk marker such as CRUMBS, it should be possible to address the question of which are the membrane domains at which dCERT controls PIP2 levels. If the sole mechanism of action of dCERT is via disruption of ER-PM MCS then only the apical rhabdomere membrane PIP2 should be affected leaving the stalk membrane and basolateral membrane unaffected.

Thank you very much for raising this specific point.

The analysis of RDGB localization should be done in mosaic dcert1 retinas, which will be more convincing with internal control for each comparison. In addition, the phalloidin staining in Figure 2J shows distinct patterns of adherens junctions, indicating that the wildtype and dcert1 were imaged at different focal planes.

We understand that having mosaics is an alternative an elegant way to perform a a side by side analysis of control and mutant. However this would require significant investment of time and effort, perhaps beyond the scope of this study. If we were to perform a mosaic analysis, this would compromise our ERG analysis since ERG is an extracellular recording We feel that this is beyond the scope of this study and perhaps may not be necessary as such (see below).

In the revision we will present equivalent sections of control and dcert1 taken from the nuclear plane of the photoreceptor. This should resolve the reviewer’s concerns.

The significance of ceramide species levels in dcert1 and GMR>CPESRNAi needs to be explained better. Do certain alterations represent accumulation of ceramides in the ER?

Species level analysis of changes in ceramides reveal that elevations in dcert1 are seen mainly in the short chain ceramides (14 and 16 carbon chains). These most likely represent the short chain ceramides synthesised in the ER and accumulating due to the block in further metabolism to PE-Cer due to depletion in CPES.

Species level analysis of changes in ceramides reveal that in dcert1 there is a ceramide transport related defect leading to elevation, primarily, in the short chain ceramides (14 and 16 carbon chains), and this selective supply defect leads to a reduction in PE-Cer levels, with a maximum change in the ratio of short-chain Cer:PE Cer (Figure 3A-D). Though there is no apparent change in the total ceramide level the species specific elevation in the ceramides disturb the fine -balance between the short-chain ceramides and the long and very-long chain ceramides. As the function of long and very-long chain ceramides are implicated in dendrite development and neuronal morphology (doi: 10.1371/journal.pgen.1011880), therefore this alteration in the fine balance between different ceramide species probably impacts the integrity and fluidity of the membrane environment. On the other hand it leads to a possibility of a defined function of the short-chain ceramides in electrical responses to light signalling in the eye, especially with respect to the PE-ceramides that are reduced by around 50%.

In contrast the GMR>CPESRNAi leads to more of a substrate accumulation showing ceramide increase (14, 16, 18, 20 carbon chains) and decrease in PE-Cer levels (Figure 4D, E). In this case Cer accumulation is due to the block in further metabolism to PE-Cer arising from depletion in CPES.

We will include this in the discussion of a revised version.

The suppression by lace is interpreted as evidence that the reduced ERG amplitude in dcert1 is caused by ceramide accumulation in the ER. This interpretation seems preliminary as lace may interact with dcert genetically by other mechanisms.

The dcert1 mutant exhibits increased levels of short-chain ceramides (Fig 3B), whereas the lace heterozygous mutant (laceK05305/+) displays reduced short-chain ceramide levels (Supp Fig 2B). In the laceK05305/+; dcert1 double mutant, ceramide levels are lower than those observed in the dcert1 mutant alone (Supp Fig 2B), indicating a partial genetic rescue of the elevated ceramide phenotype.

Furthermore, through multiple independent genetic manipulations that modulate ceramide metabolism (alterations of dcert, cpes and lace), we consistently observe that increased ceramide levels correlate with a reduction in ERG amplitude, suggesting that ceramide accumulation negatively impacts photoreceptor function. Taken together, these observations indicate that the reduction in ceramide levels in the laceK05305/+; dcert1 double mutant likely contributes to the suppression of the ERG defect observed in the dcert1 mutant.

The authors show that ERG amplitude is reduced in GMR>CPESRNAi. While this phenocopying is consistent with the reduced ERG amplitude in dcert1 being caused by reduced production of PE-ceramide, GMR>CPESRNAi also shows an increase in total ceramide level. Could this support the hypothesis that reduced ERG amplitude is caused by an accumulation of ceramide elsewhere? In addition, is the ERG amplitude reduction in GMR>CPESRNAi sensitive to lace?

We agree that in addition to reduced PE-Ceramide, the elevated ceramide levels in GMR>CPESi could contribute to the eye phenotype. We will introduce lace heterozygous mutant in the GMR>CPESi background to test the contribution of elevated ceramide levels in the *GMR>CPESi * background and incorporate the data in the revision. Thank you for this suggestion.

Along the same line, while the total ceramide level is significantly reduced in lace heterozygotes, is the PE-ceramide level also reduced? If yes, wouldn't this be contradictory to PE-ceramide production being important for ERG amplitude?

Mass spec measurements show that levels of PE-Cer were not reduced in lacek05305/+ compared to wild type. This data will be included in the revised manuscript. However, the ERG amplitude of these flies and also in those with lace depletion using two independent RNAi lines were not reduced.

What is the explanation and significance for the age-dependent deterioration of ERG amplitude in dcert1? Likewise, the significance of no retinal degeneration is not clearly presented.

There could be multiple reasons for the age dependent deterioration of the ERG amplitude, in the absence of retinal degeneration. Drosophila phototransduction cascade depends heavily on ATP production. The age dependent reduction in ATP synthesis could lead to deterioration in the ERG amplitude. These may include instability of the DRMs due to reduced PE-Cer, lower ATP levels due to mitochondrial dysfunction, an perhaps others. A previous study has shown that ATP production is highly reduced along with oxidative stress and metabolic dysfunction in dcert1 flies aged to 10 days and beyond (PMID: 17592126). The same study has also found no neuronal degeneration in dcert1 that phenocopies absence of photoreceptor degeneration in the present study. We will attempt a few experiments to rule in or rule out the these and revise the discussion accordingly.

The rescue of dcert1 phenotype by the expression of human CERT is a nice result. In addition to demonstrating a functional conservation, it allows a determination of CERT protein localization. However, the quality of images in Figure 6D should be improved. The phalloidin staining was rather poor, and the CNX99A in the lower panel was over-exposed, generating bleed-through signals at the rhabdomeres. In addition, the localization of hCERT should be explored further. For instance, does hCERT colocalize with RDGB? Is the hCERT localization altered in lace or GMR>CPESRNAi background?

As indicated in response to reviewer 1:

We will perform additional IHC experiments to

• Co-localize hCERT with an ER-PM MCS marker, e.g RDGB in wild type flies
• Co-localize hCERT with VAP-A that is enriched at the ER-PM MCS. This should help to determine if there are MCS and non-MCS pools of hCERT in these cells. marker, e.g RDGB in wild type flies
• Test if there is a pool of hCERT, in these cells that also localizes (or not) with the Golgi marker Golgin 84. These will be included in the revision to strengthen this important point.

We will also attempt to perform hCERT localization in lace or GMR>CPESRNAi background

Minor comments: 1. In Line 128, Df(732) should be Df(3L)BSC732.

Changes will be incorporated in the main manuscript.

GMR-SMSrRNAi shows an increase in ERG peak amplitude. Is there an explanation for this?

GMR-SMSrRNAi did show slight increase in ERG peak amplitude but was not statistically significant.

Reviewer #2 (Significance (Required)):

Significance As CERT mutations are implicated in human learning disability, a better understanding of CERT function in neuronal cells is certainly of interest. While the link between ceramide transport and phospholipase signaling is novel and interesting, this paper does not clearly explain the mechanism. In addition, as the ERG were measured long after the retinal cells were deficient in CERT or CPES, it is difficult to assess whether the observed phenotype is a primary defect. Furthermore, the quality of some images needs to be improved. Thus, I feel the manuscript in its current form is too preliminary.

We thank reviewer for highlighting the importance and significance of our work in the light of recent studies of CERT function in ID. As with all genetic studies it is difficult to completely disentangle the role of a gene during development from a role only in the adult. However, we will attempt to perhaps use the GAL80ts system to uncouple these two potential components of CERT function in photoreceptors. The goal will be to determine if CERT has a specific role only in adult photoreceptors or if this is coupled to a developmental role. Since ID is as a neurodevelopmental disorder, a developmental role for CERT would be equally interesting.

As previously indicated images will be improved bearing in mind the reviewer comments.

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

Summary: Lipid transfer proteins (LTPs) shuttle lipids between organelle membranes at membrane contact sites (MCSs). While extensive biochemical and cell culture studies have elucidated many aspects of LTP function, their in vivo physiological roles are only beginning to be understood. In this manuscript, the authors investigate the physiological role of the ceramide transfer protein (CERT) in Drosophila adult photoreceptors-a model previously employed by this group to study LTP function at ER-PM contact sites under physiological conditions. Using a combination of genetic, biochemical, and physiological approaches, they analyze a protein-null mutant of dcert. They show that loss of dcert causes a reduction in electrical response to light with progressive decrease in electroretinogram (ERG) amplitude with age but no retinal degeneration. Lipidomic analysis shows that while the total levels of ceramides are not changed in dcert mutants, they do observe significant change in certain species of ceramides and depletion of downstream metabolite phosphoethanolamine ceramide (PE-Cer). Using fluorescent biosensors, the authors demonstrate reduced PIP2 levels at the plasma membrane, unchanged basal PI4P levels and slower resynthesis kinetics of both lipids following depletion. Electron microscopy and immunolabeling further reveal a reduced density of ER-PM MCSs and mislocalization of the MCS-resident lipid transfer protein RDGB. Genetic interaction studies with lace and RNAi-mediated knockdown of CPES support the conclusion that both ER ceramide accumulation and PM PE-Cer depletion contribute to the observed defects in dcert mutants. In addition, detergent-resistant membrane fractionation indicates altered plasma membrane organization in the absence of dcert. The study also reports upregulation of unfolded protein response transcripts, including IRE1 and PERK, suggesting increased ER stress. Finally, expression of human CERT rescues the reduced electrical response, demonstrating functional conservation across species. Overall the manuscript is well written that builds on established work and experiments are technically rigorous. The results are clearly presented and provide valuable insights into the physiological role of CERT.

Major comments: 1.The reduced ERG amplitude appears to be the central phenotype associated with the loss of dcert, and most of the experiments in this manuscript effectively build a mechanistic framework to explain this observation. However, the experiments addressing detergent-resistant membrane domains (DRMs) and the unfolded protein response (UPR) seem somewhat disconnected from the main focus of the study. The DRM and UPR data feel peripheral and could benefit from few experiments for functional linkage to the ERG defect or should be moved to supplementary.

We agree with the reviewer that further experiments are needed to link the DRM data to the ERG defects. That would need specific biochemical alteration at the PM to modulate PE-Cer species and their effect on scaffolding proteins required for phototransduction (that is beyond the scope of the present study). We will consider moving these to the supplementary section as suggested by the reviewer.

2.The changes in ceramide species and reduction in PE-Cer are key findings of the study. These results should be further validated by performing a genetic rescue using the BAC or hCERT fly line to confirm that the lipidomic changes are specifically due to loss of CERT function.

Thank you for this comment. We will include this in the revised manuscript.

3.Figure 2B-C and 2E-F: Representative images corresponding to the quantified data should be included to illustrate the changes in PIP2 and PI4P reporters. Given that the fluorescence intensity of the PIP2 reporter at the PM is reduced in the dcert mutant relative to control, the authors should also verify that the reporter is expressed at comparable levels across genotypes.

• As mentioned by the reviewer we will include representative images alongside our quantified data both of the basal ones and that of the kinetic study.

• Western blot of reporters (PH-PLCd::GFP and P4M::GFP) across genotypes will be added to the revised manuscript. 4.Figure 2J-K: The partial mislocalization of RDGB represents an important observation that could mechanistically explain the reduced resynthesis of PI4P and PIP2 and consequently, the decreased ERG amplitude in dcert mutants. However, this result requires further validation. First, the authors should confirm whether this mislocalization is specific to RDGB by performing co-staining with another ER-PM MCS marker, such as VAP-A, to assess whether overall MCS organization is disrupted. Second, the quantification of RDGB enrichment at ER-PM MCSs should be refined. From the representative images, RDGB appears redistributed toward the photoreceptor cell body, but the presented quantification does not clearly reflect this shift. The authors should therefore include an analysis comparing RDGB levels in the cell body versus the submicrovillar region across genotypes. This analysis should be repeated for similar experiments across the study. Additionally, the total RDGB protein level should be quantified and reported. Finally, since RDGB mislocalization could directly contribute to the decreased ERG amplitude, it would be valuable to test whether overexpression of RDGB in dcert mutants can rescue the ERG phenotype.

• In our ultrastructural studies (Fig. 2H, 2I and Sup. Fig. 1A, 1B) we did see reduction in PM-SMC MCS that was corroborated with RDGB staining.

• Comparative ratio analysis of RDGB localisation at ER-PM MCS vs cell body will be included in the manuscript for all RDGB staining.
• We have done western analysis for total RDGB protein level in ROR and dcert1. This data will be included in the revised manuscript.
• This is a very interesting suggestion and we will test if RDGB overexpression can rescue ERG phenotype in dcert1.

5.Figure 3F and I-J: Inclusion of appropriate WT and laceK05205/+ controls is necessary to allow proper interpretation of the results. These controls would strengthen the conclusions regarding the functional relationship between dcert and lace.

Changes will be incorporated as per the suggestion.

6.Figure 5C: The representative images shown here appear to contradict the findings described in Figure 2A. In Figure 5C, Rhodopsin 1 levels seem markedly reduced in the dcert mutants, whereas the text states that Rh1 levels are comparable between control and mutant photoreceptors. The authors should replace or reverify the representative images to ensure that they accurately reflect the conclusions presented in the text.

We will reverify the representative images and changes will be accordingly incorporated.

7.Figure 6D: The reported localization of hCERT to ER-PM MCSs is a key and potentially insightful observation, as it suggests the subcellular site of dcert activity in photoreceptors. However, the representative images provided are not sufficiently conclusive to support this claim. The authors should validate hCERT localization by co-staining with established markers like RDGB for ER-PM CNX99A for the ER and a Golgi marker since mammalian CERT is classically localized to ER-Golgi interfaces. Optionally, the authors could also quantify the relative distribution of hCERT among these compartments to provide a clearer assessment of its subcellular localization.

As indicated in response to reviewer 1:

We will perform additional IHC experiments to

• Co-localize hCERT with an ER-PM MCS marker, e.g RDGB in wild type flies
• Co-localize hCERT with VAP-A that is enriched at the ER-PM MCS. This should help to determine if there are MCS and non-MCS pools of hCERT in these cells. marker, e.g RDGB in wild type flies
• Test if there is a pool of hCERT, in these cells that also localizes (or not) with the Golgi marker Golgin 84. These will be included in the revision to strengthen this important point.

Minor comments: 1.In the first paragraph of introduction, authors should consider citing few of the key MCS literature.

Additional literature will be included as per the suggestion.

2.Line 132: data not shown is not acceptable. Authors should consider presenting the findings in the supplemental figure.

Data will be added in supplement as per the suggestion.

3.The authors should include a comprehensive table or Excel sheet summarizing all statistical analyses. This should include the sample size, type of statistical test used and exact p-values. Providing this information will improve the transparency, reproducibility and overall rigor of the study.

We will provide all the statistical analyses in mentioned format as per the suggestion.

4.The materials and methods section can be reorganized to include citation for flystocks which do not have stock number or RRIDs if the stocks were previously described but are not available from public repositories. They should expand on the details of various quantification methods used in the study. Finally including a section of Statistical analyses would further enhance transparency and reproducibility

• Stock details will be added wherever missing as per the suggestion.
• Statistical analyses section will be included in the material and methods. **Referee cross-commenting**

1.I concur with Reviewer 1 regarding the need for more detailed reporting of statistical analyses.

We will perform multiple comparisons with mentioned data and incorporate in the revised manuscript.

2.I also agree with Reviewer 3 that the discussion should be expanded to address the age-dependent deterioration of ERG amplitude observed in the dcert mutants. This progressive decline could provide valuable insight into the long-term requirement of CERT function and signaling capacity at the photoreceptor membrane.

Expanded discussion on the age dependent ERG amplitude decline will be incorporated in the discussion as per the suggestion.

Reviewer #3 (Significance (Required)):

This study explores the physiological function of CERT, a LTP localized at MCSs in Drosophila photoreceptors and uncovers a novel role in regulating plasma membrane PE-Cer levels and GPCR-mediated signaling. These findings significantly advances our understanding of how CERT-mediated lipid transport regulates G-protein coupled phospholipase C signaling in vivo. This work also highlights Drosophila photoreceptors as a powerful system to analyze the physiological significance of lipid-dependent signaling processes. This work will be of interest to researchers in neuronal cell biology, membrane dynamics and lipid signaling community. This review is based on my expertise in neuronal cell biology.

We thank the reviewer for appreciating the significance of our work from a neuroscience perspective.

• *

3. Description of the revisions that have already been incorporated in the transferred manuscript

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

• *

4. Description of analyses that authors prefer not to carry out

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

• *

We can address all reviewer points in the revision. However, we will not be able to perform a mosaic analysis of the impact of dcert1 mutant in the retina. We feel this is beyond the scope of this revision. In our response, we have highlighted how controls included in the revision offset the need for a mosaic analysis at this stage.

Author response:

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

Reviewer #1 (Public review):

The authors present exciting new experimental data on the antigenic recognition of 78 H3N2 strains (from the beginning of the 2023 Northern Hemisphere season) against a set of 150 serum samples. The authors compare protection profiles of individual sera and find that the antigenic effect of amino acid substitutions at specific sites depends on the immune class of the sera, differentiating between children and adults. Person-to-person heterogeneity in the measured titers is strong, specifically in the group of children's sera. The authors find that the fraction of sera with low titers correlates with the inferred growth rate using maximum likelihood regression (MLR), a correlation that does not hold for pooled sera. The authors then measure the protection profile of the sera against historical vaccine strains and find that it can be explained by birth cohort for children. Finally, the authors present data comparing pre- and post- vaccination protection profiles for 39 (USA) and 8 (Australia) adults. The data shows a cohort-specific vaccination effect as measured by the average titer increase, and also a virus-specific vaccination effect for the historical vaccine strains. The generated data is shared by the authors and they also note that these methods can be applied to inform the bi-annual vaccine composition meetings, which could be highly valuable.

Thanks for this nice summary of our paper.

The following points could be addressed in a revision:

(1) The authors conclude that much of the person-to-person and strain-to-strain variation seems idiosyncratic to individual sera rather than age groups. This point is not yet fully convincing. While the mean titer of an individual may be idiosyncratic to the individual sera, the strain-to-strain variation still reveals some patterns that are consistent across individuals (the authors note the effects of substitutions at sites 145 and 275/276). A more detailed analysis, removing the individual-specific mean titer, could still show shared patterns in groups of individuals that are not necessarily defined by the birth cohort.

As the reviewer suggests, we normalized the titers for all sera to the geometric mean titer for each individual in the US-based pre-vaccination adults and children. This is only for the 2023-circulating viral strains. We then faceted these normalized titers by the same age groups we used in Figure 6, and the resulting plot is shown. Although there are differences among virus strains (some are better neutralized than others), there are not obvious age group-specific patterns (eg, the trends in the two facets are similar). This observation suggests that at least for these relatively closely related recent H3N2 strains, the strain-to-strain variation does not obviously segregate by age group. Obviously, it is possible (we think likely) that there would be more obvious age-group specific trends if we looked at a larger swath of viral strains covering a longer time range (eg, over decades of influenza evolution). We have added the new plots shown as a Supplemental Figure 6 in the revised manuscript.

(2) The authors show that the fraction of sera with a titer 138 correlates strongly with the inferred growth rate using MLR. However, the authors also note that there exists a strong correlation between the MLR growth rate and the number of HA1 mutations. This analysis does not yet show that the titers provide substantially more information about the evolutionary success. The actual relation between the measured titers and fitness is certainly more subtle than suggested by the correlation plot in Figure 5. For example, the clades A/Massachusetts and A/Sydney both have a positive fitness at the beginning of 2023, but A/Massachusetts has substantially higher relative fitness than A/Sydney. The growth inference in Figure 5b does not appear to map that difference, and the antigenic data would give the opposite ranking. Similarly, the clades A/Massachusetts and A/Ontario have both positive relative fitness, as correctly identified by the antigenic ranking, but at quite different times (i.e., in different contexts of competing clades). Other clades, like A/St. Petersburg are assigned high growth and high escape but remain at low frequency throughout. Some mention of these effects not mapped by the analysis may be appropriate.

Thanks for the nice summary of our findings in Figure 5. However, the reviewer is misreading the growth charts when they say that A/Massachusetts/18/2022 has a substantially higher fitness than A/Sydney/332/2023. Figure 5a (reprinted at left panel) shows the frequency trajectory of different variants over time. While A/Massachusetts/18/2022 reaches a higher frequency than A/Sydney/332/2023, the trajectory is similar and the reason that A/Massachusetts/18/2022 reached a higher max frequency is that it started at a higher frequency at the beginning of 2023. The MLR growth rate estimates differ from the maximum absolute frequency reached: instead, they reflect how rapidly each strain grows relative to others. In fact, A/Massachusetts/18/2022 and A/Sydney/332/2023 have similar growth rates, as shown in Supplemental Figure 6b (reprinted at right). Similarly, A/Saint-Petersburg/RII-166/2023 starts at a low initial frequency but then grows even as A/Massachusetts/18/2022 and A/Sydney/332/2023 are declining, and so has a higher growth rate than both of those. 

In the revised manuscript, we have clarified how viral growth rates are estimated from frequency trajectories, and how growth rate differs from max frequency in the text below:

“To estimate the evolutionary success of different human H3N2 influenza strains during 2023, we used multinomial logistic regression, which analyzes strain frequencies over time to calculate strain-specific relative growth rates [51–53]. There were sufficient sequencing counts to reliably estimate growth rates in 2023 for 12 of the HAs for which we measured titers using our sequencing-based neutralization assay libraries (Figure 5a,b and Supplemental Figure 9a,b). Note that these growth rates estimate how rapidly each strain grows relative to the other strains, rather than the absolute highest frequency reached by each strain “.  

(3) For the protection profile against the vaccine strains, the authors find for the adult cohort that the highest titer is always against the oldest vaccine strain tested, which is A/Texas/50/2012. However, the adult sera do not show an increase in titer towards older strains, but only a peak at A/Texas. Therefore, it could be that this is a virus-specific effect, rather than a property of the protection profile. Could the authors test with one older vaccine virus (A/Perth/16/2009?) whether this really can be a general property?

We are interested in studying immune imprinting more thoroughly using sequencing-based neutralization assays, but we note that the adults in the cohorts we studied would have been imprinted with much older strains than included in this library. As this paper focuses on the relative fitness of contemporary strains with minor secondary points regarding imprinting, these experiments are beyond the scope of this study. We’re excited for future work (from our group or others) to explore these points by making a new virus library with strains from multiple decades of influenza evolution. 

Reviewer #2 (Public review):

This is an excellent paper. The ability to measure the immune response to multiple viruses in parallel is a major advancement for the field, which will be relevant across pathogens (assuming the assay can be appropriately adapted). I only have a few comments, focused on maximising the information provided by the sera.

Thanks very much!

Firstly, one of the major findings is that there is wide heterogeneity in responses across individuals. However, we could expect that individuals' responses should be at least correlated across the viruses considered, especially when individuals are of a similar age. It would be interesting to quantify the correlation in responses as a function of the difference in ages between pairs of individuals. I am also left wondering what the potential drivers of the differences in responses are, with age being presumably key. It would be interesting to explore individual factors associated with responses to specific viruses (beyond simply comparing adults versus children).

We thank the reviewer for this interesting idea. We performed this analysis (and the related analyses described) and added this as a new Supplemental Figure 7, which is pasted after the response to the next related comment by the reviewer. 

For 2023-circulating strains, we observed basically no correlation between the strength of correlation between pairs of sera and the difference in age between those pairs of sera (Supplemental Figure 7), which was unsurprising given the high degree of heterogeneity between individual sera (Figure 3, Supplemental Figure 6, and Supplemental Figure 8). For vaccine strains, there is a moderate negative correlation only in the children, but not in the adults or the combined group of adults and children. This could be because the children are younger with limited and potentially more similar vaccine and exposure histories than the adults. It could also be because the children are overall closer in age than the adults.

Relatedly, is the phylogenetic distance between pairs of viruses associated with similarity in responses?

For 2023-circulating strains, across sera cohorts we observed a weak-to-moderate correlation between the strength of correlation between the neutralizing titers across all sera to pairs of viruses and the Hamming distances between virus pairs. For the same comparison with vaccine strains, we observed moderate correlations, but this must be caveated with the slightly larger range of Hamming distances between vaccine strains. Notably, many of the points on the negative correlation slope are a mix of egg- and cell-produced vaccine strains from similar years, but there are some strain comparisons where the same year’s egg- and cell-produced vaccine strains correlate poorly.

Figure 5C is also a really interesting result. To be able to predict growth rates based on titers in the sera is fascinating. As touched upon in the discussion, I suspect it is really dependent on the representativeness of the sera of the population (so, e.g., if only elderly individuals provided sera, it would be a different result than if only children provided samples). It may be interesting to compare different hypotheses - so e.g., see if a population-weighted titer is even better correlated with fitness - so the contribution from each individual's titer is linked to a number of individuals of that age in the population. Alternatively, maybe only the titers in younger individuals are most relevant to fitness, etc.

We’re very interested in these analyses, but suggest they may be better explored in subsequent works that could sample more children, teenagers and adults across age groups. Our sera set, as the reviewer suggests, may be under-powered to perform the proposed analysis on subsetted age groups of our larger age cohorts. 

In Figure 6, the authors lump together individuals within 10-year age categories - however, this is potentially throwing away the nuances of what is happening at individual ages, especially for the children, where the measured viruses cross different groups. I realise the numbers are small and the viruses only come from a small numbers of years, however, it may be preferable to order all the individuals by age (y-axis) and the viral responses in ascending order (x-axis) and plot the response as a heatmap. As currently plotted, it is difficult to compare across panels

This is a good suggestion. In the revised manuscript we have included a heatmap of the children and pre-vaccination adults, ordered by the year of birth of each individual, as Supplemental figure 8. That new figure is also pasted in this response.

Reviewer #3 (Public review):

The authors use high-throughput neutralisation data to explore how different summary statistics for population immune responses relate to strain success, as measured by growth rate during the 2023 season. The question of how serological measurements relate to epidemic growth is an important one, and I thought the authors present a thoughtful analysis tackling this question, with some clear figures. In particular, they found that stratifying the population based on the magnitude of their antibody titres correlates more with strain growth than using measurements derived from pooled serum data. However, there are some areas where I thought the work could be more strongly motivated and linked together. In particular, how the vaccine responses in US and Australia in Figures 6-7 relate to the earlier analysis around growth rates, and what we would expect the relationship between growth rate and population immunity to be based on epidemic theory.

Thank you for this nice summary. This reviewer also notes that the text related to figures 6 and 7 are more secondary to the main story presented in figures 3-5. The main motivation for including figures 6 and 7 were to demonstrate the wide-ranging applications of sequencing-based neutralization data. We have tried to clarify this with the following minor text revisions, which do not add new content but we hope smooth the transition between results sections. 

While the preceding analyses demonstrated the utility of sequencing-based neutralization assays for measuring titers of currently circulating strains, our library also included viruses with HAs from each of the H3N2 influenza Northern Hemisphere vaccine strains from the last decade (2014 to 2024, see Supplemental Table 1). These historical vaccine strains cover a much wider span of evolutionary diversity that the 2023-circulating strains analyzed in the preceding sections (Figure 2a,b and Supplemental Figure 2b-e). For this analysis, we focused on the cell-passaged strains for each vaccine, as these are more antigenically similar to their contemporary circulating strains than the egg-passaged vaccine strains since they lack the mutations that arise during growth of viruses in eggs [55–57] (Supplemental Table 1). 

Our sequencing-based assay could also be used to assess the impact of vaccination on neutralization titers against the full set of strains in our H3N2 library. To do this, we analyzed matched 28-day post-vaccination samples for each of the above-described 39 pre-vaccination samples from the cohort of adults based in the USA (Table 1). We also analyzed a smaller set of matched pre- and post-vaccination sera samples from a cohort of eight adults based in Australia (Table 1). Note that there are several differences between these cohorts: the USA-based cohort received the 2023-2024 Northern Hemisphere egg-grown vaccine whereas the Australia-based cohort received the 2024 Southern Hemisphere cell-grown vaccine, and most individuals in the USA-based cohort had also been vaccinated in the prior season whereas most individuals in the Australia-based cohort had not. Therefore, multiple factors could contribute to observed differences in vaccine response between the cohorts.

Reviewer #3 (Recommendations for the authors):

Main comments:

(1) The authors compare titres of the pooled sera with the median titres across individual sera, finding a weak correlation (Figure 4). I was therefore interested in the finding that geometric mean titre and median across a study population are well correlated with growth rate (Supplemental Figure 6c). It would be useful to have some more discussion on why estimates from a pool are so much worse than pooled estimates.

We thank this reviewer for this point. We would clarify that pooling sera is the equivalent of taking the arithmetic mean of the individual sera, rather than the geometric mean or median, which tends to bias the measurements of the pool to the outliers within the pool. To address this reviewer’s point, we’ve added the following text to the manuscript:

“To confirm that sera pools are not reflective of the full heterogeneity of their constituent sera, we created equal volume pools of the children and adult sera and measured the titers of these pools using the sequencing-based neutralization assay. As expected, neutralization titers of the pooled sera were always higher than the median across the individual constituent sera, and the pool titers against different viral strains were only modestly correlated with the median titers across individual sera (Figure 4). The differences in titers across strains were also compressed in the serum pools relative to the median across individual sera (Figure 4). The failure of the serum pools to capture the median titers of all the individual sera is especially dramatic for the children sera (Figure 4) because these sera are so heterogeneous in their individual titers (Figure 3b). Taken together, these results show that serum pools do not fully represent individual-level heterogeneity, and are similar to taking the arithmetic mean of the titers for a pool of individuals, which tends to be biased by the highest titer sera”.

(2) Perhaps I missed it, but are growth rates weekly growth rates? (I assume so?)

The growth rates are relative exponential growth rates calculated assuming a serial interval of 3.6 days. We also added clarifying language and a citation for the serial growth interval to the methods section:

The analysis performing H3 HA strain growth rate estimates using the evofr[51] package is at https://github.com/jbloomlab/flu_H3_2023_seqneut_vs_growth. Briefly, we sought to make growth rate estimates for the strains in 2023 since this was the same timeframe when the sera were collected. To achieve this, we downloaded all publicly-available H3N2 sequences from the GISAID[88] EpiFlu database, filtering to only those sequences that closely matched a library HA1 sequence (within one HA1 amino-acid mutation) and were collected between January 2023 and December 2023. If a sequence was within one HA1 amino-acid mutation of multiple library HA1 proteins then it was assigned to the closest one; if there were multiple equally close matches then it was assigned fractionally to each match. We only made growth rate estimates for library strains with at least 80 sequencing counts (Supplemental Figure 9a), and ignored counts for sequences that did not match a library strain (equivalent results were obtained if we instead fit a growth rate for these sequences as an “other” category). We then fit multinomial logistic regression models using the evofr[51] package assuming a serial interval of 3.6 days[101]  to the strain counts. For the plot in Figure 5a the frequencies are averaged over a 14-day sliding window for visual clarity, but the fits were to the raw sequencing counts. For most of the analyses in this paper we used models based on requiring 80 sequencing counts to make an estimate for strain growth rates, and counting a sequence as a match if it was within one amino-acid mutation; see https://jbloomlab.github.io/flu_H3_2023_seqneut_vs_growth/ for comparable analyses using different reasonable sequence count cutoffs (e.g., 60, 50, 40 and 30, as depicted in Supplemental Figure 9).  Across sequence cutoffs, we found that the fraction of individuals with low neutralization titers and number of HA1 mutations correlated strongly with these MLR-estimated strain growth rates.

(3)  I found Figure 3 useful in that it presents phylogenetic structure alongside titres, to make it clearer why certain clusters of strains have a lower response. In contrast, I found it harder to meaningfully interpret Figure 7a beyond the conclusion that vaccines lead to a fairly uniform rise in titre. Do the 275 or 276 mutations that seem important for adults in Figure 3 have any impact?

We are certainly interested in the questions this reviewer raises, and in trying to understand how well a seasonal vaccine protects against the most successful influenza variants that season. However, these post-vaccination sera were taken when neutralizing titers peak ~30 days after vaccination. Because of this, in the larger cohort of US-based post-vaccination adults, the median titers across sera to most strains appear uniformly high. In the Australian-based post-vaccination adults, there was some strain-to-strain variation in median titers across sera, but of course this must be caveated with the much smaller sample size. It might be more relevant to answer this question with longitudinally sampled sera, when titers begin to wane in the following months.

(4)  It could be useful to define a mechanistic relationship about how you would expect susceptibility (e.g. fraction with titre < X, where X is a good correlate) to relate to growth via the reproduction number: R = R0 x S. For example, under the assumption the generation interval G is the same for all, we have R = exp(r*G), which would make it possible to make a prediction about how much we would expect the growth rate to change between S = 0.45 and 0.6, as in Fig 5c. This sort of brief calculation (or at least some discussion) could add some more theoretical underpinning to the analysis, and help others build on the work in settings with different fractions with low titres. It would also provide some intuition into whether we would expect relationships to be linear.

This is an interesting idea for future work! However, the scope of our current study is to provide these experimental data and show a correlation with growth; we hope this can be used to build more mechanistic models in future.

(5) A key conclusion from the analysis is that the fraction above a threshold of ~140 is particularly informative for growth rate prediction, so would it be worth including this in Figure 6-7 to give a clearer indication of how much vaccination reduces contribution to strain growth among those who are vaccinated? This could also help link these figures more clearly with the main analysis and question.

Although our data do find ~140 to be the threshold that gives max correlation with growth rate, we are not comfortable strongly concluding 140 is a correlate of protection, as titers could influence viral fitness without completely protecting against infection. In addition, inspection of Figure 5d shows that while ~140 does give the maximal correlation, a good correlation is observed for most cutoffs in the range from ~40 to 200, so we are not sure how robustly we can be sure that ~140 is the optimal threshold.

(6)  In Figure 5, the caption doesn't seem to include a description for (e).

Thank you to the reviewer for catching this – this is fixed now.

(7)  The US vs Australia comparison could have benefited from more motivation. The authors conclude ,"Due to the multiple differences between cohorts we are unable to confidently ascribe a cause to these differences in magnitude of vaccine response" - given the small sample sizes, what hypotheses could have been tested with these data? The comparison isn't covered in the Discussion, so it seems a bit tangential currently.

Thank you to the reviewer for this comment, but we should clarify our aim was not to directly compare US and Australian adults. We are interested in regional comparisons between serum cohorts, but did not have the numbers to adequately address those questions here. This section (and the preceding question) were indeed both intended to be tangential to the main finding, and hopefully this will be clarified with our text additions in response to Reviewer #3’s public reviews.

Author response:

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

Reviewer #1 (Public Review):

This study presents an exploration of PPGL tumour bulk transcriptomics and identifies three clusters of samples (labeled as subtypes C1-C3). Each subtype is then investigated for the presence of somatic mutations, metabolism-associated pathways and inflammation correlates, and disease progression. The proposed subtype descriptions are presented as an exploratory study. The proposed potential biomarkers from this subtype are suitably caveated and will require further validation in PPGL cohorts together with a mechanistic study.  

The first section uses WGCNA (a method to identify clusters of samples based on gene expression correlations) to discover three transcriptome-based clusters of PPGL tumours. The second section inspects a previously published snRNAseq dataset, and labels some of the published cells as subtypes C1, C2, C3 (Methods could be clarified here), among other cells labelled as immune cell types. Further details about how the previously reported single-nuclei were assigned to the newly described subtypes C1-C3 require clarification.

Thank you for your valuable suggestion. In response to the reviewer’s request for further clarification on “how previously published single-nuclei data were assigned to the newly defined C1-C3 subtypes,” we have provided additional methodological details in the revised manuscript (lines 103-109). Specifically, we aggregated the single-nucleus RNA-seq data to the sample level by summing gene counts across nuclei to generate pseudo-bulk expression profiles. These profiles were then normalized for library size, log-transformed (log1p), and z-scaled across samples. Using genesets scores derived from our earlier WGCNA analysis of PPGLs, we defined transcriptional subtypes within the Magnus cohort (Supplementary Figure. 1C). We further analyzed the single-nucleus data by classifying malignant (chromaffin) nuclei as C1, C2, or C3 based on their subtype scores, while non-malignant nuclei (including immune, stromal, endothelial, and others) were annotated using canonical cell-type markers (Figure. 4A). 

The tumour samples are obtained from multiple locations in the body (Figure 1A). It will be important to see further investigation of how the sample origin is distributed among the C1C3 clusters, and whether there is a sample-origin association with mutational drivers and disease progression.

Thank you for your valuable suggestion. In the revised manuscript (lines 74-79), Figure. 1A, Table S1 and Supplementary Figure. 1A, we harmonized anatomic site annotations from our PPGL cohort and the TCGA cohort and analyzed the distribution of tumor origin (adrenal vs extra-adrenal) across subtypes. The site composition is essentially uniform across C1-C3— approximately 75% pheochromocytoma (PC) and 25% paraganglioma (PG)—with only minimal variation. Notably, the proportion of extra-adrenal origin (paraganglioma origin) is slightly higher in the C1 subtype (see Supplementary Figure 1A), which aligns with the biological characteristics of tumors from this anatomical site, which typically exhibit more aggressive behavior.

Reviewer #2 (Public Review):

A study that furthers the molecular definition of PPGL (where prognosis is variable) and provides a wide range of sub-experiments to back up the findings. One of the key premises of the study is that identification of driver mutations in PPGL is incomplete and that compromises characterisation for prognostic purposes. This is a reasonable starting point on which to base some characterisation based on different methods. The cohort is a reasonable size, and a useful validation cohort in the form of TCGA is used. Whilst it would be resource-intensive (though plausible given the rarity of the tumour type) to perform RNA-seq on all PPGL samples in clinical practice, some potential proxies are proposed.

We sincerely thank the reviewer for their positive assessment of our study’s rationale. We fully agree that RNA sequencing for all PPGL samples remains resource-intensive in current clinical practice, and its widespread application still faces feasibility challenges. It is precisely for this reason that, after defining transcriptional subtypes, we further focused on identifying and validating practical molecular markers and exploring their detectability at the protein level.

In this study, we validated key markers such as ANGPT2, PCSK1N, and GPX3 using immunohistochemistry (IHC), demonstrating their ability to effectively distinguish among molecular subtypes (see Figure. 5). This provides a potential tool for the clinical translation of transcriptional subtyping, similar to the transcription factor-based subtyping in small cell lung cancer where IHC enables low-cost and rapid molecular classification.

It should be noted that the subtyping performance of these markers has so far been preliminarily validated only in our internal cohort of 87 PPGL samples. We agree with the reviewer that largerscale, multi-center prospective studies are needed in the future to further establish the reliability and prognostic value of these markers in clinical practice.

The performance of some of the proxy markers for transcriptional subtype is not presented.

We agree with your comment regarding the need to further evaluate the performance of proxy markers for transcriptional subtyping. In our study, we have in fact taken this point into full consideration. To translate the transcriptional subtypes into a clinically applicable classification tool, we employed a linear regression model to compare the effect values (β values) of candidate marker genes across subtypes (Supplementary Figure. 1D-F). Genes with the most significant β values and statistical differences were selected as representative markers for each subtype.

Ultimately, we identified ANGPT2, PCSK1N, and GPX3—each significantly overexpressed in subtypes C1, C2, and C3, respectively, and exhibiting the most pronounced β values—as robust marker genes for these subtypes (Figure. 5A and Supplementary Figure. 1D-F). These results support the utility of these markers in subtype classification and have been thoroughly validated in our analysis.

There is limited prognostic information available.

Thank you for your valuable suggestion. In this exploratory revision, we present the available prognostic signal in Figure. 5C. Given the current event numbers and follow-up time, we intentionally limited inference. We are continuing longitudinal follow-up of the PPGL cohort and will periodically update and report mature time-to-event analyses in subsequent work.

Reviewer #1 (Recommendations for the authors):

There is no deposition reference for the RNAseq transcriptomics data. Have the data been deposited in a suitable data repository?

Thank you for your valuable suggestion. We have updated the Data availability section (lines 508–511) to clarify that the bulk-tissue RNA-seq datasets generated in this study are available from the corresponding author upon reasonable request.

In the snRNAseq analysis of existing published data, clarify how cells were labelled as "C1", "C2", "C3", alongside cells labelled by cell type (the latter is described briefly in the Methods).

Thank you for your valuable suggestion. In response to the reviewer’s request for further clarification on “how previously published single-nuclei data were assigned to the newly defined C1-C3 subtypes,” we have provided additional methodological details in the revised manuscript (lines 103-109). Specifically, we aggregated the single-nucleus RNA-seq data to the sample level by summing gene counts across nuclei to generate pseudo-bulk expression profiles. These profiles were then normalized for library size, log-transformed (log1p), and z-scaled across samples. Using genesets scores derived from our earlier WGCNA analysis of PPGLs, we defined transcriptional subtypes within the Magnus cohort (Supplementary Figure. 1C). We further analyzed the single-nucleus data by classifying malignant (chromaffin) nuclei as C1, C2, or C3 based on their subtype scores, while non-malignant nuclei (including immune, stromal, endothelial, and others) were annotated using canonical cell-type markers (Figure. 4A).

Package versions should be included (e.g., CellChat, monocle2).

We greatly appreciate your comments and have now added a dedicated “Software and versions” subsection in Methods. Specifically, we report Seurat (v4.4.0), sctransform (v0.4.2), CellChat (v2.2.0), monocle (v2.36.0; monocle2), pheatmap (v1.0.13), clusterProfiler (v4.16.0), survival (v3.8.3), and ggplot2 (v3.5.2) (lines 514-516). We also corrected a typographical error (“mafools” → “maftools”) (lines 463).

Reviewer #2 (Recommendations for the authors):

It would be helpful to provide a little more detail on the clinical composition of the cohort (e.g., phaeo vs paraganglioma, age, etc.) in the text, acknowledging that this is done in Figure 1.

Thank you for your valuable suggestion. In the revision, we added Table S1 that provides a detailed summary of the clinical composition of the PPGL cohort. Specifically, we report the numbers and proportions (Supplementary Figure. 1A) of pheochromocytoma (PC) versus paraganglioma (PG), further subclassifying PG into head and neck (HN-PG), retroperitoneal (RPPG), and bladder (BC-PG).

How many of each transcriptional subtype had driver mutations (germline or somatic)? This is included in the figures but would be worth mentioning in the text. Presumably, some of these may be present but not detected (e.g., non-coding variants), and this should be commented on. It is feasible that if methods to detect all the relevant genomic markers were improved, then the rate of tumours without driver mutations would be less and their prognostic utility would be more comprehensive.

Thank you for your valuable suggestion. In the revision (lines 113–116), we now report the prevalence of driver mutations (germline or somatic) overall and by transcriptional subtype. We analyzed variant data across 84 PPGL-relevant genes from 179 tumors in the TCGA cohort and 30 tumors in Magnus’s cohort (Fig. 2A; Table S2). High-frequency genes were consistent with known biology—C1 enriched for [e.g., VHL/SDHB], C2 for [e.g., RET/HRAS], and C3 for [e.g., SDHA/SDHD]. We also note that a subset of tumors lacked an identifiable driver, which likely reflects current assay limitations (e.g., non-coding or structural variants, subclonality, and purity effects). Broader genomic profiling (deep WGS/long-read, RNA fusion, methylation) would be expected to reduce the “driver-negative” fraction and further enhance the prognostic utility of these classifiers.

ANGPT2 provides a reasonable predictive capacity for the C1 subtype as defined by the ROC AUC. What was the performance of the PCSK1N and GPX3 as markers of the other subtypes?

We agree with your comment regarding the need to further evaluate the performance of proxy markers for transcriptional subtyping, and we have supplemented the analysis with ROC and AUC values for two additional parameters (Author response image 1 , see below). Furthermore, in our study, we have in fact taken this point into full consideration. To translate the transcriptional subtypes into a clinically applicable classification tool, we employed a linear regression model to compare the effect values (β values) of candidate marker genes across subtypes (Supplementary Figure. 1D-F). Genes with the most significant β values and statistical differences were selected as representative markers for each subtype.

Ultimately, we identified ANGPT2, PCSK1N, and GPX3—each significantly overexpressed in subtypes C1, C2, and C3, respectively, and exhibiting the most pronounced β values—as robust marker genes for these subtypes (Figure. 5A and Supplementary Figure. 1D-F). These results support the utility of these markers in subtype classification and have been thoroughly validated in our analysis.

Author response image 1.

Extended Data Figure A-B. (A) The ROC curve illustrates the diagnostic ability to distinguish PCSK1N expression in PPGLs, specifically differentiating subtype C2 from non-C2 subtypes. The red dot indicates the point with the highest sensitivity (93.1%) and specificity (82.8%). AUC, the area under the curve. (B) The ROC curve illustrates the diagnostic ability to distinguish GPX3 expression in PPGLs, specifically differentiating subtype C3 from non-C3 subtypes. The red dot indicates the point with the highest sensitivity (83.0%) and specificity (58.8%). AUC, the area under the curve.

In the discussion, I think it would be valuable to summarise existing clinical/molecular predictors in PPGL and, acknowledging that their performance may be limited, compare them to the potential of these novel classifiers.

Thank you for your valuable suggestion. We have added a concise overview of established clinical and molecular predictors in PPGL and compared them with the potential of our transcriptional classifiers. The new paragraph (Discussion, lines 315–338) now reads:

“Compared to existing clinical and molecular predictors, risk assessment in PPGL has long relied on the following indicators: clinicopathological features (e.g., tumor size, non-adrenal origin, specific secretory phenotype, Ki-67 index), histopathological scoring systems (such as PASS/GAPP), and certain genetic alterations (including high-risk markers like SDHB inactivation mutations, as well as susceptibility gene mutations in ATRX, TERT promoter, MAML3, VHL, NF1, among others). Although these metrics are highly actionable in clinical practice, they exhibit several limitations: first, current molecular markers only cover a subset of patients, and technical constraints hinder the detection of many potentially significant variants (e.g., non-coding mutations), thereby compromising the comprehensiveness of prognostic evaluation; second, histopathological scoring is susceptible to interobserver variability; furthermore, the lack of standardized detection and evaluation protocols across institutions limits the comparability and generalizability of results. Our transcriptomic classification system—comprising C1 (pseudohypoxic/angiogenic signature), C2 (kinase-signaling signature), and C3 (SDHx-related signature)—provides a complementary approach to PPGL risk assessment. These subtypes reflect distinct biological backgrounds tied to specific genetic alterations and can be approximated by measuring the expression of individual genes (e.g., ANGPT2, PCSK1N, or GPX3). This study demonstrates that the classifier offers three major advantages: first, it accurately distinguishes subtypes with coherent biological features; second, it retains significant predictive value even after adjusting for clinical covariates; third, it can be implemented using readily available assays such as immunohistochemistry. These findings suggest that integrating transcriptomic subtyping with conventional clinical markers may offer a more comprehensive and generalizable risk stratification framework. However, this strategy would require validation through multi-center prospective studies and standardization of detection protocols.”

A little more explanation of the principles behind WGCNA would be useful in the methods.

We are grateful for your comments. We have expanded the Methods to briefly explain the principles of WGCNA (lines 426-454). In short, WGCNA constructs a weighted coexpression network from normalized gene expression, identifies modules of tightly co-expressed genes, summarizes each module by its eigengene (the first principal component), and then correlates module eigengenes with phenotypes (e.g., transcriptional subtypes) to highlight biologically meaningful gene sets and candidate hub genes. We now specify our preprocessing, choice of softthresholding power to approximate scale-free topology, module detection/merging criteria, and the statistics used for module–trait association and downstream gene-set scoring. 

On line 234, I think the figure should be 5C?

We greatly appreciate your comments and Correct to Figure 5C.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Weakness:

I wonder how task difficulty and linguistic labels interact with the current findings. Based on the behavioral data, shapes with more geometric regularities are easier to detect when surrounded by other shapes. Do shape labels that are readily available (e.g., "square") help in making accurate and speedy decisions? Can the sensitivity to geometric regularity in intraparietal and inferior temporal regions be attributed to differences in task difficulty? Similarly, are the MEG oddball detection effects that are modulated by geometric regularity also affected by task difficulty?

We see two aspects to the reviewer’s remarks.

(1) Names for shapes.

On the one hand, is the question of the impact of whether certain shapes have names and others do not in our task. The work presented here is not designed to specifically test the effect of formal western education; however, in previous work (Sablé-Meyer et al., 2021), we noted that the geometric regularity effect remains present even for shapes that do not have specific names, and even in participants who do not have names for them. Thus, we replicated our main effects with both preschoolers and adults that did not attend formal western education and found that our geometric feature model remained predictive of their behavior; we refer the reader to this previous paper for an extensive discussion of the possible role of linguistic labels, and the impact of the statistics of the environment on task performance.  

What is more, in our behavior experiments we can discard data from any shape that is has a name in English and run our model comparison again. Doing so diminished the effect size of the geometric feature model, but it remained predictive of human behavior: indeed, if we removed all shapes but kite, rightKite, rustedHinge, hinge and random (i.e., more than half of our data, and shapes for which we came up with names but there are no established names), we nevertheless find that both models significantly correlate with human behavior—see plot in Author response image 1, equivalent of our Fig. 1E with the remaining shapes.

Author response image 1.

An identical analysis on the MEG leads to two noisy but significant clusters (CNN: 64.0ms to 172.0ms; then 192.0ms to 296.0ms; both p<.001: Geometric Features: 312.0ms to 364.0ms with p=.008). We have improved our manuscript thanks to the reviewer’s observation by adding a figure with the new behavior analysis to the supplementary figures and in the result section of the behavior task. We now refer to these analysis where appropriate:

(intro) “The effect appeared as a human universal, present in preschoolers, first-graders, and adults without access to formal western math education (the Himba from Namibia), and thus seemingly independent of education and of the existence of linguistic labels for regular shapes.”

(behavior results) “Finally, to separate the effect of name availability and geometric features on behavior, we replicated our analysis after removing the square, rectangle, trapezoids, rhombus and parallelogram from our data (Fig. S5D). This left us with five shapes, and an RDM with 10 entries, When regressing it in a GLM with our two models, we find that both models are still significant predictors (p<.001). The effect size of the geometric feature model is greatly reduced, yet remained significantly higher than that of the neural network model (p<.001).”

(meg results) “This analysis yielded similar clusters when performed on a subset of shapes that do not have an obvious name in English, as was the case for the behavior analysis (CNN Encoding: 64.0ms to 172.0ms; then 192.0ms to 296.0ms; both p<.001: Geometric Features: 312.0ms to 364.0ms with p=.008).”

(discussion, end of behavior section) “Previously, we only found such a significant mixture of predictors in uneducated humans (whether French preschoolers or adults from the Himba community, mitigating the possible impact of explicit western education, linguistic labels, and statistics of the environment on geometric shape representation) (Sablé-Meyer et al., 2021).”

Perhaps the referee’s point can also be reversed: we provide a normative theory of geometric shape complexity which has the potential to explain why certain shapes have names: instead of seeing shape names as the cause of their simpler mental representation, we suggest that the converse could occur, i.e. the simpler shapes are the ones that are given names.

(2) Task difficulty

On the other hand is the question of whether our effect is driven by task difficulty. First, we would like to point out that this point could apply to the fMRI task, which asks for an explicit detection of deviants, but does not apply to the MEG experiment. In MEG, participants passively looked at sequences of shapes which, for a given block, comprising many instances of a fixed standard shape and rare deviants–even if they notice deviants, they have no task related to them. Yet two independent findings validated the geometric features model: there was a large effect of geometric regularity on the MEG response to deviants, and the MEG dissimilarity matrix between standard shapes correlated with a model based on geometric features, better than with a model based on CNNs. While the response to rare deviants might perhaps be attributed to “difficulty” (assuming that, in spite of the absence of an explicit task, participants try to spot the deviants and find this self-imposed task more difficult in runs with less regular shapes), it seems very hard to explain the representational similarity analysis (RSA) findings based on difficulty. Indeed, what motivated us to use RSA analysis in both fMRI and MEG was to stop relying on the response to deviants, and use solely the data from standard or “reference” shapes, and model their neural response with theory-derived regressors.

We have updated the manuscript in several places to make our view on these points clearer:

(experiment 4) “This design allowed us to study the neural mechanisms of the geometric regularity effect without confounding effects of task, task difficulty, or eye movements.”

(figure 4, legend) “(A) Task structure: participants passively watch a constant stream of geometric shapes, one per second (presentation time 800ms). The stimuli are presented in blocks of 30 identical shapes up to scaling and rotation, with 4 occasional deviant shape. Participants do not have a task to perform beside fixating.”

Reviewer #2 (Public review):

Weakness:

Given that the primary take away from this study is that geometric shape information is found in the dorsal stream, rather than the ventral stream there is very little there is very little discussion of prior work in this area (for reviews, see Freud et al., 2016; Orban, 2011; Xu, 2018). Indeed, there is extensive evidence of shape processing in the dorsal pathway in human adults (Freud, Culham, et al., 2017; Konen & Kastner, 2008; Romei et al., 2011), children (Freud et al., 2019), patients (Freud, Ganel, et al., 2017), and monkeys (Janssen et al., 2008; Sereno & Maunsell, 1998; Van Dromme et al., 2016), as well as the similarity between models and dorsal shape representations (Ayzenberg & Behrmann, 2022; Han & Sereno, 2022).

We thank the reviewer for this opportunity to clarify our writing. We want to use this opportunity to highlight that our primary finding is not about whether the shapes of objects or animals (in general) are processed in the ventral versus or the dorsal pathway, but rather about the much more restricted domain of geometric shapes such as squares and triangles. We propose that simple geometric shapes afford additional levels of mental representation that rely on their geometric features – on top of the typical visual processing. To the best of our knowledge, this point has not been made in the above papers.

Still, we agree that it is useful to better link our proposal to previous ones. We have updated the discussion section titled “Two Visual Pathways” to include more specific references to the literature that have reported visual object representations in the dorsal pathway. Following another reviewer’s observation, we have also updated our analysis to better demonstrate the overlap in activation evoked by math and by geometry in the IPS, as well as include a novel comparison with independently published results.

Overall, to address this point, we (i) show the overlap between our “geometry” contrast (shape > word+tools+houses) and our “math” contrast (number > words); (ii) we display these ROIs side by side with ROIs found in previous work (Amalric and Dehaene, 2016), and (iii) in each math-related ROIs reported in that article, we test our “geometry” (shape > word+tools+houses) contrast and find almost all of them to be significant in both population; see Fig. S5.

Finally, within the ROIs identified with our geometry localizer, we also performed similarity analyses: for each region we extracted the betas of every voxel for every visual category, and estimated the distance (cross-validated mahalanobis) between different visual categories. In both ventral ROIs, in both populations, numbers were closer to shapes than to the other visual categories including text and Chinese characters (all p<.001). In adults, this result also holds for the right ITG (p=.021) and the left IPS (p=.014) but not the right IPS (p=.17). In children, this result did not hold in the areas.

Naturally, overlap in brain activation does not suffice to conclude that the same computational processes are involved. We have added an explicit caveat about this point. Indeed, throughout the article,  we have been careful to frame our results in a way that is appropriate given our evidence, e.g. saying “Those areas are similar to those active during number perception, arithmetic, geometric sequences, and the processing of high-level math concepts” and “The IPS areas activated by geometric shapes overlap with those active during the comprehension of elementary as well as advanced mathematical concepts”. We have rephrased the possibly ambiguous “geometric shapes activated math- and number-related areas, particular the right aIPS.” into “geometric shapes activated areas independently found to be activated by math- and number-related tasks, in particular the right aIPS”.

Reviewer #3 (Public review):

Weakness:

Perhaps the manuscript could emphasize that the areas recruited by geometric figures but not objects are spatial, with reduced processing in visual areas. It also seems important to say that the images of real objects are interpreted as representations of 3D objects, as they activate the same visual areas as real objects. By contrast, the images of geometric forms are not interpreted as representations of real objects but rather perhaps as 2D abstractions.

This is an interesting possibility. Geometric shapes are likely to draw attention to spatial dimensions (e.g. length) and to do so in a 2D spatial frame of reference rather than the 3D representations evoked by most other objects or images. However, this possibility would require further work to be thoroughly evaluated, for instance by comparing usual 3D objects with rare instances of 2D ones (e.g. a sheet of paper, a sticker etc). In the absence of such a test, we refrained from further speculation on this point.

The authors use the term "symbolic." That use of that term could usefully be expanded here.  

The reviewer is right in pointing out that “symbolic” should have been more clearly defined. We now added in the introduction:

(introduction) “[…] we sometimes refer to this model as “symbolic” because it relies on discrete, exact, rule-based features rather than continuous representations  (Sablé-Meyer et al., 2022). In this representational format, geometric shapes are postulated to be represented by symbolic expressions in a “language-of-thought”, e.g. “a square is a four-sided figure with four equal sides and four right angles” or equivalently by a computer-like program from drawing them in a Logo-like language (Sablé-Meyer et al., 2022).”

Here, however, the present experiments do not directly probe this format of a representation. We have therefore simplified our wording and removed many of our use of the word “symbolic” in favor of the more specific “geometric features”.

Pigeons have remarkable visual systems. According to my fallible memory, Herrnstein investigated visual categories in pigeons. They can recognize individual people from fragments of photos, among other feats. I believe pigeons failed at geometric figures and also at cartoon drawings of things they could recognize in photos. This suggests they did not interpret line drawings of objects as representations of objects.

The comparison of geometric abilities across species is an interesting line of research. In the discussion, we briefly mention several lines of research that indicate that non-human primates do not perceive geometric shapes in the same way as we do – but for space reasons, we are reluctant to expand this section to a broader review of other more distant species. The referee is right that there is evidence of pigeons being able to perceive an invariant abstract 3D geometric shape in spite of much variation in viewpoint (Peissig et al., 2019) – but there does not seem to be evidence that they attend to geometric regularities specifically (e.g. squares versus non-squares). Also, the referee’s point bears on the somewhat different issue of whether humans and other animals may recognize the object depicted by a symbolic drawing (e.g. a sketch of a tree). Again, humans seem to be vastly superior in this domain, and research on this topic is currently ongoing in the lab. However, the point that we are making in the present work is specifically about the neural correlates of the representation of simple geometric shapes which by design were not intended to be interpretable as representations of objects.

Categories are established in part by contrast categories; are quadrilaterals, triangles, and circles different categories?

We are not sure how to interpret the referee’s question, since it bears on the definition of “category” (Spontaneous? After training? With what criterion?). While we are not aware of data that can unambiguously answer the reviewer’s question, categorical perception in geometric shapes can be inferred from early work investigating pop-out effects in visual search, e.g. (Treisman and Gormican, 1988): curvature appears to generate strong pop-out effects, and therefore we would expect e.g. circles to indeed be a different category than, say, triangles. Similarly, right angles, as well as parallel lines, have been found to be perceived categorically (Dillon et al., 2019).

This suggests that indeed squares would be perceived as categorically different from triangles and circles. On the other hand, in our own previous work (Sablé-Meyer et al., 2021) we have found that the deviants that we generated from our quadrilaterals did not pop out from displays of reference quadrilaterals. Pop-out is probably not the proper criterion for defining what a “category” is, but this is the extent to which we can provide an answer to the reviewer’s question.

It would be instructive to investigate stimuli that are on a continuum from representational to geometric, e.g., table tops or cartons under various projections, or balls or buildings that are rectangular or triangular. Building parts, inside and out. like corners. Objects differ from geometric forms in many ways: 3D rather than 2D, more complicated shapes, and internal texture. The geometric figures used are flat, 2-D, but much geometry is 3-D (e. g. cubes) with similar abstract features.

We agree that there is a whole line of potential research here. We decided to start by focusing on the simplest set of geometric shapes that would give us enough variation in geometric regularity while being easy to match on other visual features. We agree with the reviewer that our results should hold both for more complex 2-D shapes, but also for 3-D shapes. Indeed, generative theories of shapes in higher dimensions following similar principles as ours have been devised (I. Biederman, 1987; Leyton, 2003).  We now mention this in the discussion:

“Finally, this research should ultimately be extended to the representation of 3-dimensional geometric shapes, for which similar symbolic generative models have indeed been proposed (Irving Biederman, 1987; Leyton, 2003).”

The feature space of geometry is more than parallelism and symmetry; angles are important, for example. Listing and testing features would be fascinating. Similarly, looking at younger or preferably non-Western children, as Western children are exposed to shapes in play at early ages.

We agree with the reviewer on all point. While we do not list and test the different properties separately in this work, we would like to highlight that angles are part of our geometric feature model, which includes features of “right-angle” and “equal-angles” as suggested by the reviewer.

We also agree about the importance of testing populations with limited exposure to formal training with geometric shapes. This was in fact a core aspect of a previous article of ours which tests both preschoolers, and adults with no access to formal western education – though no non-Western children (Sablé-Meyer et al., 2021). It remains a challenge to perform brain-imaging studies in non-Western populations (although see Dehaene et al., 2010; Pegado et al., 2014).

What in human experience but not the experience of close primates would drive the abstraction of these geometric properties? It's easy to make a case for elaborate brain processes for recognizing and distinguishing things in the world, shared by many species, but the case for brain areas sensitive to processing geometric figures is harder. The fact that these areas are active in blind mathematicians and that they are parietal areas suggests that what is important is spatial far more than visual. Could these geometric figures and their abstract properties be connected in some way to behavior, perhaps with fabrication and construction as well as use? Or with other interactions with complex objects and environments where symmetry and parallelism (and angles and curvature--and weight and size) would be important? Manual dexterity and fabrication also distinguish humans from great apes (quantitatively, not qualitatively), and action drives both visual and spatial representations of objects and spaces in the brain. I certainly wouldn't expect the authors to add research to this already packed paper, but raising some of the conceptual issues would contribute to the significance of the paper.

We refrained from speculating about this point in the previous version of the article, but share some of the reviewers’ intuitions about the underlying drive for geometric abstraction. As described in (Dehaene, 2026; Sablé-Meyer et al., 2022), our hypothesis, which isn’t tested in the present article, is that the emergence of a pervasive ability to represent aspects of the world as compact expressions in a mental “language-of-thought” is what underlies many domains of specific human competence, including some listed by the reviewer (tool construction, scene understanding) and our domain of study here, geometric shapes.

Recommendations for the Authors:

Reviewer #1 (Recommendations for the authors):

Overall, I enjoyed reading this paper. It is clearly written and nicely showcases the amount of work that has gone into conducting all these experiments and analyzing the data in sophisticated ways. I also thought the figures were great, and I liked the level of organization in the GitHub repository and am looking forward to seeing the shared data on OpenNeuro. I have some specific questions I hope the authors can address.

(1) Behavior

- Looking at Figure 1, it seemed like most shapes are clustering together, whereas square, rectangle, and maybe rhombus and parallelogram are slightly more unique. I was wondering whether the authors could comment on the potential influence of linguistic labels. Is it possible that it is easier to discard the intruder when the shapes are readily nameable versus not?

This is an interesting observation, but the existence of names for shapes does not suffice to explain all of our findings ; see our reply to the public comment.

(2) fMRI

- As mentioned in the public review, I was surprised that the authors went with an intruder task because I would imagine that performance depends on the specific combination of geometric shapes used within a trial. I assume it is much harder to find, for example, a "Right Hinge" embedded within "Hinge" stimuli than a "Right Hinge" amongst "Squares". In addition, the rotation and scaling of each individual item should affect regular shapes less than irregular shapes, creating visual dissimilarities that would presumably make the task harder. Can the authors comment on how we can be sure that the differences we pick up in the parietal areas are not related to task difficulty but are truly related to geometric shape regularities?

Again, please see our public review response for a larger discussion of the impact of task difficulty. There are two aspects to answering this question.

First, the task is not as the reviewer describes: the intruder task is to find a deviant shape within several slightly rotated and scaled versions of the regular shape it came from. During brain imaging, we did not ask participants to find an exemplar of one of our reference shape amidst copies of another, but rather a deviant version of one shape against copies of its reference version. We only used this intruder task with all pairs of shapes to generate the behavioral RSA matrix.

Second, we agree that some of the fMRI effect may stem from task difficulty, and this motivated our use of RSA analysis in fMRI, and a passive MEG task. RSA results cannot be explained by task difficulty.

Overall, we have tried to make the limitations of the fMRI design, and the motivation for turning to passive presentation in MEG, clearer by stating the issues more clearly when we introduce experiment 4:

“The temporal resolution of fMRI does not allow to track the dynamic of mental representations over time. Furthermore, the previous fMRI experiment suffered from several limitations. First, we studied six quadrilaterals only, compared to 11 in our previous behavioral work. Second, we used an explicit intruder detection, which implies that the geometric regularity effect was correlated with task difficulty, and we cannot exclude that this factor alone explains some of the activations in figure 3C (although it is much less clear how task difficulty alone would explain the RSA results in figure 3D). Third, the long display duration, which was necessary for good task performance especially in children, afforded the possibility of eye movements, which were not monitored inside the 3T scanner and again could have affected the activations in figure 3C.”

- How far in the periphery were the stimuli presented? Was eye-tracking data collected for the intruder task? Similar to the point above, I would imagine that a harder trial would result in more eye movements to find the intruder, which could drive some of the differences observed here.

A 1-degree bar was added to Figure 3A, which faithfully illustrates how the stimuli were presented in fMRI. Eye-tracking data was not collected during fMRI. Although the participants were explicitly instructed to fixate at the center of the screen and avoid eye movements, we fully agree with the referee that we cannot exclude that eye movements were present, perhaps more so for more difficult displays, and would therefore have contributed to the observed fMRI activations in experiment 3 (figure 3C). We now mention this limitation explicity at the end of experiment 3. However, crucially, this potential problem cannot apply to the MEG data. During the MEG task, the stimuli were presented one by one at the center of screen, without any explicit task, thus avoiding issues of eye movements. We therefore consider the MEG geometrical regularity effect, which comes at a relatively early latency (starting at ~160 ms) and even in a passive task, to provide the strongest evidence of geometric coding, unaffected by potential eye movement artefacts. 

- I was wondering whether the authors would consider showing some un-thresholded maps just to see how widespread the activation of the geometric shapes is across all of the cortex.

We share the uncorrected threshold maps in Fig. S3. for both adults and children in the category localizer, copied here as well. For the geometry task, most of the clusters identified are fairly big and survive cluster-corrected permutations; the uncorrected statistical maps look almost fully identical to the one presented in Fig. 3 (p<.001 map).

- I'm missing some discussion on the role of early visual areas that goes beyond the RSA-CNN comparison. I would imagine that early visual areas are not only engaged due to top-down feedback (line 258) but may actually also encode some of the geometric features, such as parallel lines and symmetry. Is it feasible to look at early visual areas and examine what the similarity structure between different shapes looks like?

If early visual areas encoded the geometric features that we propose, then even early sensor-level RSA matrices should show a strong impact of geometric features similarity, which is not what we find (figure 4D). We do, however, appreciate the referee’s request to examine more closely how this similarity structure looks like. We now provide a movie showing the significant correlation between neural activity and our two models (uncorrected participants); indeed, while the early occipital activity (around 110ms) is dominated by a significant correlation with the CNN model, there are also scattered significant sources associated to the symbolic model around these timepoints already.

To test this further, we used beamformers to reconstruct the source-localized activity in calcarine cortex and performed an RSA analysis across that ROI. We find that indeed the CNN model is strongly significant at t=110ms (t=3.43, df=18, p=.003) while the geometric feature model is not (t=1.04, df=18, p=.31), and the CNN is significantly above the geometric feature model (t=4.25, df=18, p<.001). However, this result is not very stable across time, and there are significant temporal clusters around these timepoints associated to each model, with no significant cluster associated to a CNN > geometric (CNN: significant cluster from 88ms to 140ms, p<.001 in permutation based with 10000 permutations; geometric features has a significant cluster from 80ms to 104ms, p=.0475; no significant cluster on the difference between the two).

(3) MEG

- Similar to the fMRI set, I am a little worried that task difficulty has an effect on the decoding results, as the oddball should pop out more in more geometric shapes, making it easier to detect and easier to decode. Can the authors comment on whether it would matter for the conclusions whether they are decoding varying task difficulty or differences in geometric regularity, or whether they think this can be considered similarly?

See above for an extensive discussion of the task difficulty effect. We point out that there is no task in the MEG data collection part. We have clarified the task design by updating our Fig. 4. Additionally, the fact that oddballs are more perceived more or less easily as a function of their geometric regularity is, in part, exactly the point that we are making – but, in MEG, even in the absence of a task of looking for them.

- The authors discuss that the inflated baseline/onset decoding/regression estimates may occur because the shapes are being repeated within a mini-block, which I think is unlikely given the long ISIs and the fact that the geometric features model is not >0 at onset. I think their second possible explanation, that this may have to do with smoothing, is very possible. In the text, it said that for the non-smoothed result, the CNN encoding correlates with the data from 60ms, which makes a lot more sense. I would like to encourage the authors to provide readers with the unsmoothed beta values instead of the 100-ms smoothed version in the main plot to preserve the reason they chose to use MEG - for high temporal resolution!

We fully agree with the reviewer and have accordingly updated the figures to show the unsmoothed data (see below). Indeed, there is now no significant CNN effect before ~60 ms (up to the accuracy of identifying onsets with our method).

- In Figure 4C, I think it would be useful to either provide error bars or show variability across participants by plotting each participant's beta values. I think it would also be nice to plot the dissimilarity matrices based on the MEG data at select timepoints, just to see what the similarity structure is like.

Following the reviewer’s recommendation, we plot the timeseries with SEM as shaded area, and thicker lines for statistically significant clusters, and we provide the unsmoothed version in figure Fig. 4. As for the dissimilarity matrices at select timepoints, this has now been added to figure Fig. 4.

- To evaluate the source model reconstruction, I think the reader would need a little more detail on how it was done in the main text. How were the lead fields calculated? Which data was used to estimate the sources? How are the models correlated with the source data?

We have imported some of the details in the main text as follows (as well as expanding the methods section a little):

“To understand which brain areas generated these distinct patterns of activations, and probe whether they fit with our previous fMRI results, we performed a source reconstruction of our data. We projected the sensor activity onto each participant's cortical surfaces estimated from T1-images. The projection was performed using eLORETA and emptyroom recordings acquired on the same day to estimate noise covariance, with the default parameters of mne-bids-pipeline. Sources were spaced using a recursively subdivided octahedron (oct5). Group statistics were performed after alignement to fsaverage. We then replicated the RSA analysis […]”

- In addition to fitting the CNN, which is used here to model differences in early visual cortex, have the authors considered looking at their fMRI results and localizing early visual regions, extracting a similarity matrix, and correlating that with the MEG and/or comparing it with the CNN model?

We had ultimately decided against comparing the empirical similarity matrices from the MEG and fMRI experiments, first because the stimuli and tasks are different, and second because this would not be directly relevant to our goal, which is to evaluate whether a geometric-feature model accounts for the data. Thus, we systematically model empirical similarity matrices from fMRI and from MEG with our two models derived from different theories of shape perception in order to test predictions about their spatial and temporal dynamic. As for comparing the similarity matrix from early visual regions in fMRI with that predicted by the CNN model, this is effectively visible from our Fig. 3D where we perform searchlight RSA analysis and modeling with both the CNN and the geometric feature model; bilaterally, we find a correlation with the CNN model, although it sometimes overlap with predictions from the geometric feature model as well. We now include a section explaining this reasoning in appendix:

“Representational similarity analysis also offers a way to directly compared similarity matrices measured in MEG and fMRI, thus allowing for fusion of those two modalities and tentatively assigning a “time stamp” to distinct MRI clusters. However, we did not attempt such an analysis here for several reasons. First, distinct tasks and block structures were used in MEG and fMRI. Second, a smaller list of shapes was used in fMRI, as imposed by the slower modality of acquisition. Third, our study was designed as an attempt to sort out between two models of geometric shape recognition. We therefore focused all analyses on this goal, which could not have been achieved by direct MEG-fMRI fusion, but required correlation with independently obtained model predictions.”

Minor comments

- It's a little unclear from the abstract that there is children's data for fMRI only.

We have reworded the abstract to make this unambiguous

- Figures 4a & b are missing y-labels.

We can see how our labels could be confused with (sub-)plot titles and have moved them to make the interpretation clearer.

- MEG: are the stimuli always shown in the same orientation and size?

They are not, each shape has a random orientation and scaling. On top of a task example at the top of Fig. 4, we have now included a clearer mention of this in the main text when we introduce the task:

“shapes were presented serially, one at a time, with small random changes in rotation and scaling parameters, in miniblocks with a fixed quadrilateral shape and with rare intruders with the bottom right corner shifted by a fixed amount (Sablé-Meyer et al., 2021)”

- To me, the discussion section felt a little lengthy, and I wonder whether it would benefit from being a little more streamlined, focused, and targeted. I found that the structure was a little difficult to follow as it went from describing the result by modality (behavior, fMRI, MEG) back to discussing mostly aspects of the fMRI findings.

We have tried to re-organize and streamline the discussion following these comments.

Then, later on, I found that especially the section on "neurophysiological implementation of geometry" went beyond the focus of the data presented in the paper and was comparatively long and speculative.

We have reexamined the discussion, but the citation of papers emphasizing a representation of non-accidental geometric properties in non-human animals was requested by other commentators on our article; and indeed, we think that they are relevant in the context of our prior suggestion that the composition of geometric features might be a uniquely human feature – these papers suggest that individual features may not, and that it is therefore compositionality which might be special to the human brain. We have nevertheless shortened it.

Furthermore, we think that this section is important because symbolic models are often criticized for lack of a plausible neurophysiological implementation. It is therefore important to discuss whether and how the postulated symbolic geometric code could be realized in neural circuits. We have added this justification to the introduction of this section.

Reviewer #2 (Recommendations for the authors):

(1) If the authors want to specifically claim that their findings align with mathematical reasoning, they could at least show the overlap between the activation maps of the current study and those from prior work.

This was added to the fMRI results. See our answers to the public review.

(2) I wonder if the reason the authors only found aIPS in their first analysis (Figure 2) is because they are contrasting geometric shapes with figures that also have geometric properties. In other words, faces, objects, and houses also contain geometric shape information, and so the authors may have essentially contrasted out other areas that are sensitive to these features. One indication that this may be the case is that the geometric regularity effect and searchlight RSA (Figure 3) contains both anterior and posterior IPS regions (but crucially, little ventral activity). It might be interesting to discuss the implications of these differences.

Indeed, we cannot exclude that the few symmetries, perpendicularity and parallelism cues that can be presented in faces, objects or houses were processed as such, perhaps within the ventral pathway, and that these representations would have been subtracted out. We emphasize that our subtraction isolates the geometrical features that are present in simple regular geometric shapes, over and above those that might exist in other categories. We have added this point to the discussion:

“[… ] For instance, faces possess a plane of quasi-symmetry, and so do many other man-made tools and houses. Thus, our subtraction isolated the geometrical features that are present in simple regular geometric shapes (e.g. parallels, right angles, equality of length) over and above those that might already exist, in a less pure form, in other categories.”

(3) I had a few questions regarding the MEG results.

a. I didn't quite understand the task. What is a regular or oddball shape in this context? It's not clear what is being decoded. Perhaps a small example of the MEG task in Figure 4 would help?

We now include an additional sub-figure in Fig. 4 to explain the paradigm. In brief: there is no explicit task, participants are simply asked to fixate. The shapes come in miniblocks of 30 identical reference shapes (up to rotation and scaling), among which some occasional deviant shapes randomly appear (created by moving the corner of the reference shape by some amount).

b. In Figure 4A/B they describe the correlation with a 'symbolic model'. Is this the same as the geometric model in 4C?

It is. We have removed this ambiguity by calling it “geometric model” and setting its color to the one associated to this model thought the article.

c. The author's explanation for why geometric feature coding was slower than CNN encoding doesn't quite make sense to me. As an explanation, they suggest that previous studies computed "elementary features of location or motor affordance", whereas their study work examines "high-level mathematical information of an abstract nature." However, looking at the studies the authors cite in this section, it seems that these studies also examined the time course of shape processing in the dorsal pathway, not "elementary features of location or motor affordance." Second, it's not clear how the geometric feature model reflects high-level mathematical information (see point above about claiming this is related to math).

We thank the referee for pointing out this inappropriate phrase, which we removed. We rephrased the rest of the paragraph to clarify our hypothesis in the following way:

“However, in this work, we specifically probed the processing of geometric shapes that, if our hypothesis is correct, are represented as mental expressions that combine geometrical and arithmetic features of an abstract categorical nature, for instance representing “four equal sides” or “four right angles”. It seems logical that such expressions, combining number, angle and length information, take more time to be computed than the first wave of feedforward processing within the occipito-temporal visual pathway, and therefore only activate thereafter.”

One explanation may be that the authors' geometric shapes require finer-grained discrimination than the object categories used in prior studies. i.e., the odd-ball task may be more of a fine-grained visual discrimination task. Indeed, it may not be a surprise that one can decode the difference between, say, a hammer and a butterfly faster than two kinds of quadrilaterals.

We do not disagree with this intuition, although note that we do not have data on this point (we are reporting and modelling the MEG RSA matrix across geometric shapes only – in this part, no other shapes such as tools or faces are involved). Still, the difference between squares, rectangles, parallelograms and other geometric shapes in our stimuli is not so subtle. Furthermore, CNNs do make very fine grained distinctions, for instance between many different breeds of dogs in the IMAGENET corpus. Still, those sorts of distinctions capture the initial part of the MEG response, while the geometric model is needed only for the later part. Thus, we think that it is a genuine finding that geometric computations associated with the dorsal parietal pathway are slower than the image analysis performed by the ventral occipito-temporal pathway.

d. CNN encoding at time 0 is a little weird, but the author's explanation, that this is explained by the fact that temporal smoothed using a 100 ms window makes sense. However, smoothing by 100 ms is quite a lot, and it doesn't seem accurate to present continuous time course data when the decoding or RSA result at each time point reflects a 100 ms bin. It may be more accurate to simply show unsmoothed data. I'm less convinced by the explanation about shape prediction.

We agree. Following the reviewer’s advice, as well as the recommendation from reviewer 1, we now display unsmoothed plots, and the effects now exhibit a more reasonable timing (Figure 4D), with effects starting around ~60 ms for CNN encoding.

(4) I appreciate the author's use of multiple models and their explanation for why DINOv2 explains more variance than the geometric and CNN models (that it represents both types of features. A variance partitioning analysis may help strengthen this conclusion (Bonner & Epstein, 2018; Lescroart et al., 2015).

However, one difference between DINOv2 and the CNN used here is that it is trained on a dataset of 142 million images vs. the 1.5 million images used in ImageNet. Thus, DINOv2 is more likely to have been exposed to simple geometric shapes during training, whereas standard ImageNet trained models are not. Indeed, prior work has shown that lesioning line drawing-like images from such datasets drastically impairs the performance of large models (Mayilvahanan et al., 2024). Thus, it is unlikely that the use of a transformer architecture explains the performance of DINOv2. The authors could include an ImageNet-trained transformer (e.g., ViT) and a CNN trained on large datasets (e.g., ResNet trained on the Open Clip dataset) to test these possibilities. However, I think it's also sufficient to discuss visual experience as a possible explanation for the CNN and DINOv2 results. Indeed, young children are exposed to geometric shapes, whereas ImageNet-trained CNNs are not.

We agree with the reviewer’s observation. In fact, new and ongoing work from the lab is also exploring this; we have included in supplementary materials exactly what the reviewer is suggesting, namely the time course of the correlation with ViT and with ConvNeXT. In line with the reviewers’ prediction, these networks, trained on much larger dataset and with many more parameters, can also fit the human data as well as DINOv2. We ran additional analysis of the MEG data with ViT and ConvNeXT, which we now report in Fig. S6 as well as in an additional sentence in that section:

“[…] similar results were obtained by performing the same analysis, not only with another vision transformer network, ViT, but crucially using a much larger convolutional neural network, ConvNeXT, which comprises ~800M parameters and has been trained on 2B images, likely including many geometric shapes and human drawings. For the sake of completeness, RSA analysis in sensor space of the MEG data with these two models is provided in Fig. S6.”

We conclude that the size and nature of the training set could be as important as the architecture – but also note that humans do not rely on such a huge training set. We have updated the text, as well as Fig. S6, accordingly by updating the section now entitled “Vision Transformers and Larger Neural Networks”, and the discussion section on theoretical models.

(5) The authors may be interested in a recent paper from Arcaro and colleagues that showed that the parietal cortex is greatly expanded in humans (including infants) compared to non-human primates (Meyer et al., 2025), which may explain the stronger geometric reasoning abilities of humans.

A very interesting article indeed! We have updated our article to incorporate this reference in the discussion, in the section on visual pathways, as follows:

“Finally, recent work shows that within the visual cortex, the strongest relative difference in growth between human and non-human primates is localized in parietal areas (Meyer et al., 2025). If this expansion reflected the acquisition of new processing abilities in these regions, it  might explain the observed differences in geometric abilities between human and non-human primates (Sablé-Meyer et al., 2021).”

Also, the authors may want to include this paper, which uses a similar oddity task and compelling shows that crows are sensitive to geometric regularity:

Schmidbauer, P., Hahn, M., & Nieder, A. (2025). Crows recognize geometric regularity. Science Advances, 11(15), eadt3718. https://doi.org/10.1126/sciadv.adt3718

We have ongoing discussions with the authors of this work and are  have prepared a response to their findings (Sablé-Meyer and Dehaene, 2025)–ultimately, we think that this discussion, which we agree is important, does not have its place in the present article. They used a reduced version of our design, with amplified differences in the intruders. While they did not test the fit of their model with CNN or geometric feature models, we did and found that a simple CNN suffices to account for crow behavior. Thus, we disagree that their conclusions follow from their results and their conclusions. But the present article does not seem to be the right platform to engage in this discussion.

References

Ayzenberg, V., & Behrmann, M. (2022). The Dorsal Visual Pathway Represents Object-Centered Spatial Relations for Object Recognition. The Journal of Neuroscience, 42(23), 4693-4710. https://doi.org/10.1523/jneurosci.2257-21.2022

Bonner, M. F., & Epstein, R. A. (2018). Computational mechanisms underlying cortical responses to the affordance properties of visual scenes. PLoS Computational Biology, 14(4), e1006111. https://doi.org/10.1371/journal.pcbi.1006111

Bueti, D., & Walsh, V. (2009). The parietal cortex and the representation of time, space, number and other magnitudes. Philosophical Transactions of the Royal Society B: Biological Sciences, 364(1525), 1831-1840.

Dehaene, S., & Brannon, E. (2011). Space, time and number in the brain: Searching for the foundations of mathematical thought. Academic Press.

Freud, E., Culham, J. C., Plaut, D. C., & Bermann, M. (2017). The large-scale organization of shape processing in the ventral and dorsal pathways. eLife, 6, e27576.

Freud, E., Ganel, T., Shelef, I., Hammer, M. D., Avidan, G., & Behrmann, M. (2017). Three-dimensional representations of objects in dorsal cortex are dissociable from those in ventral cortex. Cerebral Cortex, 27(1), 422-434.

Freud, E., Plaut, D. C., & Behrmann, M. (2016). 'What 'is happening in the dorsal visual pathway. Trends in Cognitive Sciences, 20(10), 773-784.

Freud, E., Plaut, D. C., & Behrmann, M. (2019). Protracted developmental trajectory of shape processing along the two visual pathways. Journal of Cognitive Neuroscience, 31(10), 1589-1597.

Han, Z., & Sereno, A. (2022). Modeling the Ventral and Dorsal Cortical Visual Pathways Using Artificial Neural Networks. Neural Computation, 34(1), 138-171. https://doi.org/10.1162/neco_a_01456

Janssen, P., Srivastava, S., Ombelet, S., & Orban, G. A. (2008). Coding of shape and position in macaque lateral intraparietal area. Journal of Neuroscience, 28(26), 6679-6690.

Konen, C. S., & Kastner, S. (2008). Two hierarchically organized neural systems for object information in human visual cortex. Nature Neuroscience, 11(2), 224-231.

Lescroart, M. D., Stansbury, D. E., & Gallant, J. L. (2015). Fourier power, subjective distance, and object categories all provide plausible models of BOLD responses in scene-selective visual areas. Frontiers in Computational Neuroscience, 9(135), 1-20. https://doi.org/10.3389/fncom.2015.00135

Mayilvahanan, P., Zimmermann, R. S., Wiedemer, T., Rusak, E., Juhos, A., Bethge, M., & Brendel, W. (2024). In search of forgotten domain generalization. arXiv Preprint arXiv:2410.08258.

Meyer, E. E., Martynek, M., Kastner, S., Livingstone, M. S., & Arcaro, M. J. (2025). Expansion of a conserved architecture drives the evolution of the primate visual cortex. Proceedings of the National Academy of Sciences, 122(3), e2421585122. https://doi.org/10.1073/pnas.2421585122

Orban, G. A. (2011). The extraction of 3D shape in the visual system of human and nonhuman primates. Annual Review of Neuroscience, 34, 361-388.

Romei, V., Driver, J., Schyns, P. G., & Thut, G. (2011). Rhythmic TMS over Parietal Cortex Links Distinct Brain Frequencies to Global versus Local Visual Processing. Current Biology, 21(4), 334-337. https://doi.org/10.1016/j.cub.2011.01.035

Sereno, A. B., & Maunsell, J. H. R. (1998). Shape selectivity in primate lateral intraparietal cortex. Nature, 395(6701), 500-503. https://doi.org/10.1038/26752

Summerfield, C., Luyckx, F., & Sheahan, H. (2020). Structure learning and the posterior parietal cortex. Progress in Neurobiology, 184, 101717. https://doi.org/10.1016/j.pneurobio.2019.101717

Van Dromme, I. C., Premereur, E., Verhoef, B.-E., Vanduffel, W., & Janssen, P. (2016). Posterior Parietal Cortex Drives Inferotemporal Activations During Three-Dimensional Object Vision. PLoS Biology, 14(4), e1002445. https://doi.org/10.1371/journal.pbio.1002445

Xu, Y. (2018). A tale of two visual systems: Invariant and adaptive visual information representations in the primate brain. Annu. Rev. Vis. Sci, 4, 311-336.

Reviewer #3 (Recommendations for the authors):

Bring into the discussion some of the issues outlined above, especially a) the spatial rather than visual of the geometric figures and b) the non-representational aspects of geometric form aspects.

We thank the reviewer for their recommendations – see our response to the public review for more details.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

This paper addresses a very interesting problem of non-centrosomal microtubule organization in developing Drosophila oocytes. Using genetics and imaging experiments, the authors reveal an interplay between the activity of kinesin-1, together with its essential cofactor Ensconsin, and microtubule organization at the cell cortex by the spectraplakin Shot, minus-end binding protein Patronin and Ninein, a protein implicated in microtubule minus end anchoring. The authors demonstrate that the loss of Ensconsin affects the cortical accumulation non-centrosomal microtubule organizing center (ncMTOC) proteins, microtubule length and vesicle motility in the oocyte, and show that this phenotype can be rescued by constitutively active kinesin-1 mutant, but not by Ensconsin mutants deficient in microtubule or kinesin binding. The functional connection between Ensconsin, kinesin-1 and ncMTOCs is further supported by a rescue experiment with Shot overexpression. Genetics and imaging experiments further implicate Ninein in the same pathway. These data are a clear strength of the paper; they represent a very interesting and useful addition to the field.

The weaknesses of the study are two-fold. First, the paper seems to lack a clear molecular model, uniting the observed phenomenology with the molecular functions of the studied proteins. Most importantly, it is not clear how kinesin-based plus-end directed transport contributes to cortical localization of ncMTOCs and regulation of microtubule length.

Second, not all conclusions and interpretations in the paper are supported by the presented data.

We thank the reviewer for recognizing the impact of this work. In response to the insightful suggestions, we performed extensive new experiments that establish a well-supported cellular and molecular model (Figure 7). The discussion has been restructured to directly link each conclusion to its corresponding experimental evidence, significantly strengthening the manuscript.

Below is a list of specific comments, outlining the concerns, in the order of appearance in the paper/figures.

Figure 1. The statement: "Ens loading on MTs in NCs and their subsequent transport by Dynein toward ring canals promotes the spatial enrichment of the Khc activator Ens in the oocyte" is not supported by data. The authors do not demonstrate that Ens is actually transported from the nurse cells to the oocyte while being attached to microtubules. They do show that the intensity of Ensconsin correlates with the intensity of microtubules, that the distribution of Ensconsin depends on its affinity to microtubules and that an Ensconsin pool locally photoactivated in a nurse cell can redistribute to the oocyte (and throughout the nurse cell) by what seems to be diffusion. The provided images suggest that Ensconsin passively diffuses into the oocyte and accumulates there because of higher microtubule density, which depends on dynein. To prove that Ensconsin is indeed transported by dynein in the microtubule-bound form, one would need to measure the residence time of Ensconsin on microtubules and demonstrate that it is longer than the time needed to transport microtubules by dynein into the oocyte; ideally, one would like to see movement of individual microtubules labelled with photoconverted Ensconsin from a nurse cell into the oocyte. Since microtubules are not enriched in the oocyte of the dynein mutant, analysis of Ensconsin intensity in this mutant is not informative and does not reveal the mechanism of Ensconsin accumulation.

As noted by Reviewer 3, the directional movement of microtubules traveling at ~140 nm/s from nurse cells toward the oocyte through Ring Canals was previously reported using a tagged Ens-MT binding domain reporter line by Lu et al. (2022). We have therefore added the citation of this crucial work in the novel version of the manuscript (lane 155-157) and removed the photo-conversion panel.

Critically, however, our study provides mechanistic insight that was missing from this earlier work: this mechanism is also crucial to enrich MAPs in the oocyte. The fact that Dynein mutants fail to enrich Ensconsin is a crucial piece of evidence: it supports a model of Ensconsin-loaded MT transport (Figure 1D-1F).

Figure 2. According to the abstract, this figure shows that Ensconsin is "maintained at the oocyte cortex by Ninein". However, the figure doesn't seem to prove it - it shows that oocyte enrichment of Ensonsin is partially dependent on Ninein, but this applies to the whole cell and not just to the cell cortex. Furthermore, it is not clear whether Ninein mutation affects microtubule density, which in turn would affect Ensconsin enrichment, and therefore, it is not clear whether the effect of Ninein loss on Ensconsin distribution is direct or indirect.

Ninein plays a critical role in Ensconsin enrichment and microtubule organization in the oocyte (new Figure 2, Figure 3, Figure S3). Quantification of total Tubulin signal shows no difference between control and Nin mutant oocytes (new Figure S3 panels A, B). We found decreased Ens enrichment in the oocyte, and Ens localization on MTs and to the cell cortex (Figure 2E, 2F, and Figure S3C and S3D).

Novel quantitative analyses of microtubule orientation at the anterior cortex, where MTs are normally preferentially oriented toward the posterior pole (Parton et al. 2011), demonstrate that Nin mutants exhibit randomized MT orientation compared to wild-type oocytes (new Figure 3C-3E).These findings establish that Ninein (although not essential) favors Ensconsin localization on MTs, Ens enrichment in the oocyte, ncMTOC cortical localization, and more robust MT orientation toward the posterior cortex. It also suggests that Ens levels in the oocyte acts as a rheostat to control Khc activation.

The observation that the aggregates formed by overexpressed Ninein accumulate other proteins, including Ensconsin, supports, though does not prove their interactions. Furthermore, there is absolutely no proof that Ninein aggregates are "ncMTOCs". Unless the authors demonstrate that these aggregates nucleate or anchor microtubules (for example, by detailed imaging of microtubules and EB1 comets), the text and labels in the figure would need to be altered.

We have modified the manuscript, we now refer to an accumulation of these components in large puncta, rather than aggregates, consistent with previous observations (Rosen et al., 2000). We acknowledge in the revised version that these puncta recruit Shot, Patronin and Ens without mentioning direct interaction (lane 218).

Importantly, we conducted a more detailed characterization of these Ninein/Shot/Patronin/Ens-containing puncta in a novel Figure S4. To rigorously assess their nucleation capacity, we analyzed Eb1-GFP-labeled MT comets, a robust readout of MT nucleation (Parton et al., 2011, Nashchekin et al., 2016). While few Eb1-positive comets occasionally emanate from these structures, confirming their identity as putative ncMTOCs, these puncta function as surprisingly weak nucleation centers (new Figure S4 E, Video S1) and, their presence does not alter overall MT architecture (new Figure S4 F). Moreover, these puncta disappear over time, are barely visible at stage 10B, they do not impair oocyte development or fertility (Figure S4 G and Table 1).

Minor comment: Note that a "ratio" (Figure 2C) is just a ratio, and should not be expressed in arbitrary units.

We have amended this point in all the figures.

Figure 3B: immunoprecipitation results cannot be interpreted because the immunoprecipitated proteins (GFP, Ens-GFP, Shot-YFP) are not shown. It is also not clear that this biochemical experiment is useful. If the authors would like to suggest that Ensconsin directly binds to Patronin, the interaction would need to be properly mapped at the protein domain level.

This is a good point: the GFP and Ens-GFP immunoprecipitated proteins are now much clearly identified on the blots and in the figure legend (new Figure 4G). Shot-YFP IP, was used as a positive control but is difficult to be detected by Western blot due to its large size (>106 Da) using conventional acrylamide gels (Nashchekin et al., 2016).

We now explicitly state that immunoprecipitations were performed at 4°C, where microtubules are fully depolymerized, thereby excluding undirect microtubule-mediated interactions. We agree with this reviewer: we cannot formally rule out interactions through bridging by other protein components. This is stated in the revised manuscript (lane 238-239).

One of the major phenotypes observed by the authors in Ens mutant is the loss of long microtubules. The authors make strong conclusions about the independence of this phenotype from the parameters of microtubule plus-end growth, but in fact, the quality of their data does not allow to make such a conclusion, because they only measured the number of EB1 comets and their growth rate but not the catastrophe, rescue or pausing frequency."Note that kinesin-1 has been implicated in promoting microtubule damage and rescue (doi: 10.1016/j.devcel.2021).In the absence of such measurements, one cannot conclude whether short microtubules arise through defects in the minus-end, plus-end or microtubule shaft regulation pathways.

We thank the reviewer for raising this important point. Our data demonstrate that microtubule (MT) nucleation and polymerization rates remain unaffected under Khc RNAi and ens mutant conditions, indicating that MT dynamics alterations must arise through alternative mechanisms.

As the reviewer suggested, recent studies on Kinesin activity and MT network regulation are indeed highly relevant. Two key studies from the Verhey and Aumeier laboratories examined Kinesin-1 gain-of-function conditions and revealed that constitutively active Kinesin-1 induces MT lattice damage (Budaitis et al., 2022). While damaged MTs can undergo self-repair, Aumeier and colleagues demonstrated that GTP-tubulin incorporation generates "rescue shafts" that promote MT rescue events (Andreu-Carbo et al., 2022). Extrapolating from these findings, loss of Kinesin-1 activity could plausibly reduce rescue shaft formation, thereby decreasing MT rescue frequency and stability. Although this hypothesis is challenging to test directly in our system, it provides a mechanistic framework for the observed reduction in MT number and stability.

Additionally, the reviewer highlighted the role of Khc in transporting the dynactin complex, an anti-catastrophe factor, to MT plus ends (Nieuwburg et al., 2017), which could further contribute to MT stabilization. This crucial reference is now incorporated into the revised Discussion.

Importantly, our work also demonstrates the contribution of Ens/Khc to ncMTOC targeting to the cell cortex. Our new quantitative analyses of MT organization (new Figure 5 B) reveal a defective anteroposterior orientation of cortical MTs in mutant conditions, pointing to a critical role for cortical ncMTOCs in organizing the MT network.

Taken together, we propose that the observed MT reduction and disorganization result from multiple interconnected mechanisms: (1) reduced rescue shaft formation affecting MT stability; (2) impaired transport of anti-catastrophe factors to MT plus ends; and (3) loss of cortical ncMTOCs, which are essential for minus-end MT stabilization and network organization. The Discussion has been revised to reflect this integrated model in a dedicated paragraph (“A possible regulation of MT dynamics in the oocyte at both plus end minus MT ends by Ens and Khc” lane 415-432).

It is important to note in that a spectraplakin, like Shot, can potentially affect different pathways, particularly when overexpressed.

We agree that Shot harbors multiple functional domains and acts as a key organizer of both actin and microtubule cytoskeletons. Overexpression of such a cytoskeletal cross-linker could indeed perturb both networks, making interpretation of Ens phenotype rescue challenging due to potential indirect effects.

To address this concern, we selected an appropriate Shot isoform for our rescue experiments that displayed similar localization to “endogenous” Shot-YFP (a genomic construct harboring shot regulatory sequences) and importantly that was not overexpressed.

Elevated expression of the Shot.L(A) isoform (see Western Blot Figure S8 A), considered as the wild-type form with two CH1 and CH2 actin-binding motifs (Lee and Kolodziej, 2002), showed abnormal localization such as strong binding to the microtubules in nurse cells and oocyte confirming the risk of gain-of-function artifacts and inappropriate conclusions (Figure S8 B, arrows).

By contrast, our rescue experiments using the Shot.L(C) isoform (that only harbors the CH2 motif) provide strong evidence against such artifacts for three reasons. First, Shot-L(C) is expressed at slightly lower levels than a Shot-YFP genomic construct (not overexpressed), and at much lower levels than Shot-L(A), despite using the same driver (Figure S8 A). Second, Shot-L(C) localization in the oocyte is similar to that of endogenous Shot-YFP, concentrating at the cell cortex (Figure S8 B, compare lower and top panels). Taken together, these controls rather suggest our rescue with the Shot-L(C) is specific.

Note that this Shot-L(C) isoform is sufficient to complement the absence of the shot gene in other cell contexts (Lee and Kolodziej, 2002).

Unjustified conclusions should be removed: the authors do not provide sufficient data to conclude that "ens and Khc oocytes MT organizational defects are caused by decreased ncMTOC cortical anchoring", because the actual cortical microtubule anchoring was not measured.

This is a valid point. We acknowledge that we did not directly measure microtubule anchoring in this study. In response, we have revised the discussion to more accurately reflect our observations. Throughout the manuscript, we now refer to "cortical microtubule organization" rather than "cortical microtubule anchoring," which better aligns with the data presented.

Minor comment: Microtubule growth velocity must be expressed in units of length per time, to enable evaluating the quality of the data, and not as a normalized value.

This is now amended in the revised version (modified Figure S7).

A significant part of the Discussion is dedicated to the potential role of Ensconsin in cortical microtubule anchoring and potential transport of ncMTOCs by kinesin. It is obviously fine that the authors discuss different theories, but it would be very helpful if the authors would first state what has been directly measured and established by their data, and what are the putative, currently speculative explanations of these data.

We have carefully considered the reviewer's constructive comments and are confident that this revised version fully addresses their concerns.

First, we have substantially strengthened the connection between the Results and Discussion sections, ensuring that our interpretations are more directly anchored in the experimental data. This restructuring significantly improves the overall clarity and logical flow of the manuscript.

Second, we have added a new comprehensive figure presenting a molecular-scale model of Kinesin-1 activation upon release of autoinhibition by Ensconsin (new Figure 7D). Critically, this figure also illustrates our proposed positive feedback loop mechanism: Khc-dependent cytoplasmic advection promotes cortical recruitment of additional ncMTOCs, which generates new cortical microtubules and further accelerates cytoplasmic transport (Figure 7 A-C). This self-amplifying cycle provides a mechanistic framework consistent with emerging evidence that cytoplasmic flows are essential for efficient intracellular transport in both insect and mammalian oocytes.

Minor comment: The writing and particularly the grammar need to be significantly improved throughout, which should be very easy with current language tools. Examples: "ncMTOCs recruitment" should be "ncMTOC recruitment"; "Vesicles speed" should be "Vesicle speed", "Nin oocytes harbored a WT growth,"- unclear what this means, etc. Many paragraphs are very long and difficult to read. Making shorter paragraphs would make the authors' line of thought more accessible to the reader.

We have amended and shortened the manuscript according to this reviewer feed-back. We have specifically built more focused paragraphs to facilitates the reading.

Significance

This paper represents significant advance in understanding non-centrosomal microtubule organization in general and in developing Drosophila oocytes in particular by connecting the microtubule minus-end regulation pathway to the Kinesin-1 and Ensconsin/MAP7-dependent transport. The genetics and imaging data are of good quality, are appropriately presented and quantified. These are clear strengths of the study which will make it interesting to researchers studying the cytoskeleton, microtubule-associated proteins and motors, and fly development.

The weaknesses of this study are due to the lack of clarity of the overall molecular model, which would limit the impact of the study on the field. Some interpretations are not sufficiently supported by data, but this can be solved by more precise and careful writing, without extensive additional experimentation.

We thank the reviewer for raising these important concerns regarding clarity and data interpretation. We have thoroughly revised the manuscript to address these issues on multiple fronts. First, we have substantially rewritten key sections to ensure that our conclusions are clearly articulated and directly supported by the data. Second, we have performed several new experiments that now allow us to propose a robust mechanistic model, presented in new figures. These additions significantly strengthen the manuscript and directly address the reviewer's concerns.

My expertise is cell biology and biochemistry of the microtubule cytoskeleton, including both microtubule-associated proteins and microtubule motors.

Reviewer #2

Evidence, reproducibility and clarity

In this manuscript, Berisha et al. investigate how microtubule (MT) organization is spatially regulated during Drosophila oogenesis. The authors identify a mechanism in which the Kinesin-1 activator Ensconsin/MAP7 is transported by dynein and anchored at the oocyte cortex via Ninein, enabling localized activation of Kinesin-1. Disruption of this pathway impairs ncMTOC recruitment and MT anchoring at the cortex. The authors combine genetic manipulation with high-resolution microscopy and use three key readouts to assess MT organization during mid-to-late oogenesis: cortical MT formation, localization of posterior determinants, and ooplasmic streaming. Notably, Kinesin-1, in concert with its activator Ens/MAP7, contributes to organizing the microtubule network it travels along. Overall, the study presents interesting findings, though we have several concerns we would like the authors to address. Ensconsin enrichment in the oocyte 1. Enrichment in the oocyte • Ensconsin is a MAP that binds MTs. Given that microtubule density in the oocyte significantly exceeds that in the nurse cells, its enrichment may passively reflect this difference. To assess whether the enrichment is specific, could the authors express a non-Drosophila MAP (e.g., mammalian MAP1B) to determine whether it also preferentially localizes to the oocyte?

To address this point, we performed a new series of experiments analyzing the enrichment of other Drosophila and non-Drosophila MAPs, including Jupiter-GFP, Eb1-GFP, and bovine Tau-GFP, all widely used markers of the microtubule cytoskeleton in flies (see new Figure S2). Our results reveal that Jupiter-GFP, Eb1-GFP, and bovine Tau-GFP all exhibit significantly weaker enrichment in the oocyte compared to Ens-GFP. Khc-GFP also shows lower enrichment. These findings indicate that MAP enrichment in the oocyte is MAP-dependent, rather than solely reflecting microtubule density or organization. Of note, we cannot exclude that microtubule post-translational modifications contribute to differential MAP binding between nurse cells and the oocyte, but this remains a question for future investigation.

The ability of ens-wt and ens-LowMT to induce tubulin polymerization according to the light scattering data (Fig. S1J) is minimal and does not reflect dramatic differences in localization. The authors should verify that, in all cases, the polymerization product in their in vitro assays is microtubules rather than other light-scattering aggregates. What is the control in these experiments? If it is just purified tubulin, it should not form polymers at physiological concentrations.

The critical concentration Cr for microtubule self-assembly in classical BRB80 buffer found by us and others is around 20 µM (see Fig. 2c in Weiss et al., 2010). Here, microtubules were assembled at 40 µM tubulin concentration, i.e., largely above the Cr. As stated in the materials and methods section, we systematically induced cooling at 4°C after assembly to assess the presence of aggregates, since those do not fall apart upon cooling. The decrease in optical density upon cooling is a direct control that the initial increase in DO is due to the formation of microtubules. Finally, aggregation and polymerization curves are widely different, the former displaying an exponential shape and the latter a sigmoid assembly phase (see Fig. 3A and 3B in Weiss et al., 2010).

Photoconversion caveatsMAPs are known to dynamically associate and dissociate from microtubules. Therefore, interpretation of the Ens photoconversion data should be made with caution. The expanding red signal from the nurse cells to the oocyte may reflect a any combination of dynein-mediated MT transport and passive diffusion of unbound Ensconsin. Notably, photoconversion of a soluble protein in the nurse cells would also result in a gradual increase in red signal in the oocyte, independent of active transport. We encourage the authors to more thoroughly discuss these caveats. It may also help to present the green and red channels side by side rather than as merged images, to allow readers to assess signal movement and spatial patterns better.

This is a valid point that mirrors the comment of Reviewers 1 and 3. The directional movement of microtubules traveling at ~140 nm/s from nurse cells toward the oocyte via the ring canals was previously reported by Lu et al. (2022) with excellent spatial resolution. Notably, this MT transport was measured using a fusion protein containing the Ens MT-binding domain. We now cite this relevant study in our revised manuscript and have removed this redundant panel in Figure 1.

Reduction of Shot at the anterior cortex• Shot is known to bind strongly to F-actin, and in the Drosophila ovary, its localization typically correlates more closely with F-actin structures than with microtubules, despite being an MT-actin crosslinker. Therefore, the observed reduction of cortical Shot in ens, nin mutants, and Khc-RNAi oocytes is unexpected. It would be important to determine whether cortical F-actin is also disrupted in these conditions, which should be straightforward to assess via phalloidin staining.

As requested by the reviewer, we performed actin staining experiments, which are now presented in a new Figure S5. These data demonstrate that the cortical actin network remains intact in all mutant backgrounds analyzed, ruling out any indirect effect of actin cytoskeleton disruption on the observed phenotypes.

MTs are barely visible in Fig. 3A, which is meant to demonstrate Ens-GFP colocalization with tubulin. Higher-quality images are needed.

The revised version now provides significantly improved images to show the different components examined. Our data show that Ens and Ninein localize at the cell cortex where they co-localize with Shot and Patronin (Figure 2 A-C). In addition, novel images show that Ens extends along microtubules (new Figure 4 A).

MT gradient in stage 9 oocytesIn ens-/-, nin-/-, and Khc-RNAi oocytes, is there any global defect in the stage 9 microtubule gradient? This information would help clarify the extent to which cortical localization defects reflect broader disruptions in microtubule polarity.

We now provide quantitative analysis of microtubule (MT) array organization in novel figures (Figure 3D and Figure 5B). Our data reveal that both Khc RNAi and ens mutant oocytes exhibit severe disruption of MT orientation toward the posterior (new Figure 5B). Importantly, this defect is significantly less pronounced in Nin-/- oocytes, which retain residual ncMTOCs at the cortex (new Figure 3D). This differential phenotype supports our model that cortical ncMTOCs are critical for maintaining proper MT orientation toward the posterior side of the oocyte.

Role of Ninein in cortical anchoringThe requirement for Ninein in cortical anchorage is the least convincing aspect of the manuscript and somewhat disrupts the narrative flow. First, it is unclear whether Ninein exhibits the same oocyte-enriched localization pattern as Ensconsin. Is Ninein detectable in nurse cells? Second, the Ninein antibody signal appears concentrated in a small area of the anterior-lateral oocyte cortex (Fig. 2A), yet Ninein loss leads to reduced Shot signal along a much larger portion of the anterior cortex (Fig. 2F)-a spatial mismatch that weakens the proposed functional relationship. Third, Ninein overexpression results in cortical aggregates that co-localize with Shot, Patronin, and Ensconsin. Are these aggregates functional ncMTOCs? Do microtubules emanate from these foci?

We now provide a more comprehensive analysis of Ninein localization. Similar to Ensconsin (Ens), endogenous Ninein is enriched in the oocyte during the early stages of oocyte development but is also detected in NCs (see modified Figure 2 A and Lasko et al., 2016). Improved imaging of Ninein further shows that the protein partially co-localizes with Ens, and ncMTOCs at the anterior cortex and with Ens-bound MTs (Figure 2B, 2C).

Importantly, loss of Ninein (Nin) only partially reduces the enrichment of Ens in the oocyte (Figure 2E). Both Ens and Kinesin heavy chain (Khc) remain partially functional and continue to target non-centrosomal microtubule-organizing centers (ncMTOCs) to the cortex (Figure 3A). In Nin-/- mutants, a subset of long cortical microtubules (MTs) is present, thereby generating cytoplasmic streaming, although less efficiently than under wild-type (WT) conditions (Figure 3F and 3G). As a non-essential gene, we envisage Ninein as a facilitator of MT organization during oocyte development.

Finally, our new analyses demonstrate that large puncta containing Ninein, Shot, Patronin, and despite their size, appear to be relatively weak nucleation centers (revised Figure S4 E and Video 1). In addition, their presence does not bias overall MT architecture (Figure S4 F) nor impair oocyte development and fertility (Figure S4 G and Table 1).

Inconsistency of Khc^MutEns rescueThe Khc^MutEns variant partially rescues cortical MT formation and restores a slow but measurable cytoplasmic flow yet it fails to rescue Staufen localization (Fig. 5). This raises questions about the consistency and completeness of the rescue. Could the authors clarify this discrepancy or propose a mechanistic rationale?

This is a good point. The cytoplasmic flows (the consequence of cargo transport by Khc on MTs) generated by a constitutively active KhcMutEns in an ens mutant condition, are less efficient than those driven by Khc activated by Ens in a control condition (Figure 6C). The rescued flow is probably not efficient enough to completely rescue the Staufen localization at stage 10.

Additionally, this KhcMutEns variant rescues the viability of embryos from Khc27 mutant germline clones oocytes but not from ens mutants (Table1). One hypothesis is that Ens harbors additional functions beyond Khc activation.

This incomplete rescue of Ens by an active Khc variant could also be the consequence of the “paradox of co-dependence”: Kinesin-1 also transport the antagonizing motor Dynein that promotes cargo transport in opposite directions (Hancock et al., 2016). The phenotype of a gain of function variant is therefore complex to interpret. Consistent with this, both KhcMutEns-GFP and KhcDhinge2 two active Khc only rescues partially centrosome transport in ens mutant Neural Stem Cells (Figure S10).

Minor points: 1. The pUbi-attB-Khc-GFP vector was used to generate the Khc^MutEns transgenic line, presumably under control of the ubiquitous ubi promoter. Could the authors specify which attP landing site was used? Additionally, are the transgenic flies viable and fertile, given that Kinesin-1 is hyperactive in this construct?

All transgenic constructs were integrated at defined genomic landing sites to ensure controlled expression levels. Specifically, both GFP-tagged KhcWT and KhcMutEns were inserted at the VK05 (attP9A) site using PhiC31-mediated integration. Full details of the landing sites are provided in the Materials and Methods section. Both transgenic flies are homozygous lethal and the transgenes are maintained over TM6B balancers.

On page 11 (Discussion, section titled "A dual Ensconsin oocyte enrichment mechanism achieves spatial relief of Khc inhibition"), the statement "many mutations in Kif5A are causal of human diseases" would benefit from a brief clarification. Since not all readers may be familiar with kinesin gene nomenclature, please indicate that KIF5A is one of the three human homologs of Kinesin heavy chain.

We clarified this point in the revised version (lane 465-466).

On page 16 (Materials and Methods, "Immunofluorescence in fly ovaries"), the sentence "Ovaries were mounted on a slide with ProlonGold medium with DAPI (Invitrogen)" should be corrected to "ProLong Gold."

This is corrected.

Significance

This study shows that enrichment of MAP7/ensconsin in the oocyte is the mechanism of kinesin-1 activation there and is important for cytoplasmic streaming and localization non-centrosomal microtubule-organizing centers to the oocyte cortex

We thank the reviewers for the accurate review of our manuscript and their positive feed-back.

Reviewer #3

Evidence, reproducibility and clarity

The manuscript of Berisha et al., investigates the role of Ensconsin (Ens), Kinesin-1 and Ninein in organisation of microtubules (MT) in Drosophila oocyte. At stage 9 oocytes Kinesin-1 transports oskar mRNA, a posterior determinant, along MT that are organised by ncMTOCs. At stage 10b, Kinesin-1 induces cytoplasmic advection to mix the contents of the oocyte. Ensconsin/Map7 is a MT associated protein (MAP) that uses its MT-binding domain (MBD) and kinesin binding domain (KBD) to recruit Kinesin-1 to the microtubules and to stimulate the motility of MT-bound Kinesin-1. Using various new Ens transgenes, the authors demonstrate the requirement of Ens MBD and Ninein in Ens localisation to the oocyte where Ens activates Kinesin-1 using its KBD. The authors also claim that Ens, Kinesin-1 and Ninein are required for the accumulation of ncMTOCs at the oocyte cortex and argue that the detachment of the ncMTOCs from the cortex accounts for the reduced localisation of oskar mRNA at stage 9 and the lack of cytoplasmic streaming at stage 10b. Although the manuscript contains several interesting observations, the authors' conclusions are not sufficiently supported by their data. The structure function analysis of Ensconsin (Ens) is potentially publishable, but the conclusions on ncMTOC anchoring and cytoplasmic streaming not convincing.

We are grateful that the regulation of Khc activity by MAP7 was well received by all reviewers. While our study focuses on Drosophila oogenesis, we believe this mechanism may have broader implications for understanding kinesin regulation across biological systems.

For the novel function of the MAP7/Khc complex in organizing its own microtubule networks through ncMTOC recruitment, we have carefully considered the reviewers' constructive recommendations. We now provide additional experimental evidence supporting a model of flux self-amplification in which ncMTOC recruitment plays a key role. It is well established that cytoplasmic flows are essential for posterior localization of cell fate determinants at stage 10B. Slow flows have also been described at earlier oogenesis stages by the groups of Saxton and St Johnston. Building on these early publications and our new experiments, we propose that these flows are essential to promote a positive feedback loop that reinforces ncMTOC recruitment and MT organization (Figure 7).

1) The main conclusion of the manuscript is that "MT advection failure in Khc and ens in late oogenesis stems from defective cortical ncMTOCs recruitment". This completely overlooks the abundant evidence that Kinesin-1 directly drives cytoplasmic streaming by transporting vesicles and microtubules along microtubules, which then move the cytoplasm by advection (Palacios et al., 2002; Serbus et al, 2005; Lu et al, 2016). Since Kinesin-1 generates the flows, one cannot conclude that the effect of khc and ens mutants on cortical ncMTOC positioning has any direct effect on these flows, which do not occur in these mutants.

We regret the lack of clarity of the first version of the manuscript and some missing references. We propose a model in which the Kinesin-1- dependent slow flows (described by Serbus/Saxton and Palacios/StJohnston) play a central role in amplifying ncMTOC anchoring and cortical MT network formation (see model in the new Figure 7).

2) The authors claim that streaming phenotypes of ens and khs mutants are due to a decrease in microtubule length caused by the defective localisation of ncMTOCs. In addition to the problem raised above, However, I am not convinced that they can make accurate measurements of microtubule length from confocal images like those shown in Figure 4. Firstly, they are measuring the length of bundles of microtubules and cannot resolve individual microtubules. This problem is compounded by the fact that the microtubules do not align into parallel bundles in the mutants. This will make the "microtubules" appear shorter in the mutants. In addition, the alignment of the microtubules in wild-type allows one to choose images in which the microtubule lie in the imaging plane, whereas the more disorganized arrangement of the microtubules in the mutants means that most microtubules will cross the imaging plane, which precludes accurate measurements of their length.

As mentioned by Reviewer 4, we have been transparent with the methodology, and the limitations that were fully described in the material and methods section.

Cortical microtubules in oocytes are highly dynamic and move rapidly, making it technically impossible to capture their entire length using standard Z-stack acquisitions. We therefore adopted a compromise approach: measuring microtubules within a single focal plane positioned just below the oocyte cortex. This strategy is consistent with established methods in the field, such as those used by Parton et al. (2011) to track microtubule plus-end directionality. To avoid overinterpretation, we explicitly refer to these measurements as "minimum detectable MT length," acknowledging that microtubules may extend beyond the focal plane, particularly at stage 10, where long, tortuous bundles frequently exit the plane of focus. These methodological considerations and potential biases are clearly described in the Materials and Methods section and the text now mentions the possible disorganization of the MT network in the mutant conditions (lane 272-273).

In this revised version, we now provide complementary analyses of MT network organization.Beyond length measurements (and the mentioned limitations), we also quantified microtubule network orientation at stage 9, assessing whether cortical microtubules are preferentially oriented toward the posterior axis as observed in controls (revised Figure 3D and Figure 5B). While this analysis is also subject to the same technical limitations, it reveals a clear biological difference: microtubules exhibit posterior-biased orientation in control oocytes similar to a previous study (Parton et al., 2011) but adopt a randomized orientation in Nin-/-, ens, and Khc RNAi-depleted oocytes (revised Figure 3D and Figure 5B).

Taken together, these complementary approaches, despite their technical constraints, provide convergent evidence for the role of the Khc/Ens complex in organizing cortical microtubule networks during oogenesis.

3) "To investigate whether the presence of these short microtubules in ens and Khc RNAi oocytes is due to defects in microtubule anchoring or is also associated with a decrease in microtubule polymerization at their plus ends, we quantified the velocity and number of EB1comets, which label growing microtubule plus ends (Figure S3)." I do not understand how the anchoring or not of microtubule minus ends to the cortex determines how far their plus ends grow, and these measurements fall short of showing that plus end growth is unaffected. It has already been shown that the Kinesin-1-dependent transport of Dynactin to growing microtubule plus ends increases the length of microtubules in the oocyte because Dynactin acts as an anti-catastrophe factor at the plus ends. Thus, khc mutants should have shorter microtubules independently of any effects on ncMTOC anchoring. The measurements of EB1 comet speed and frequency in FigS2 will not detect this change and are not relevant for their claims about microtubule length. Furthermore, the authors measured EB1 comets at stage 9 (where they did not observe short MT) rather than at stage 10b. The authors' argument would be better supported if they performed the measurements at stage 10b.

We thank the reviewer for raising this important point. The short microtubule (MT) length observed at stage 10B could indeed result from limited plus-end growth. Unfortunately, we were unable to test this hypothesis directly: strong endogenous yolk autofluorescence at this stage prevented reliable detection of Eb1-GFP comets, precluding velocity measurements.

At least during stage 9, our data demonstrate that MT nucleation and polymerization rates are not reduced in both KhcRNAi and ens mutant conditions, indicating that the observed MT alterations must arise through alternative mechanisms.

In the discussion, we propose the following interconnected explanations, supported by recent literature and the reviewers’ suggestions:

1- Reduced MT rescue events. Two seminal studies from the Verhey and Aumeier laboratories have shown that constitutively active Kinesin-1 induces MT lattice damage (Budaitis et al., 2022), which can be repaired through GTP-tubulin incorporation into "rescue shafts" that promote MT rescue (Andreu-Carbo et al., 2022). Extrapolating from these findings, loss of Kinesin-1 activity could plausibly reduce rescue shaft formation, thereby decreasing MT stability. While challenging to test directly in our system, this mechanism provides a plausible framework for the observed phenotype.

2- Impaired transport of stabilizing factors. As that reviewer astutely points out, Khc transports the dynactin complex, an anti-catastrophe factor, to MT plus ends (Nieuwburg et al., 2017). Loss of this transport could further compromise MT plus end stability. We now discuss this important mechanism in the revised manuscript.

3- Loss of cortical ncMTOCs. Critically, our new quantitative analyses (revised Figure 3 and Figure 5) also reveal defective anteroposterior orientation of cortical MTs in mutant conditions. These experiments suggest that Ens/Khc-mediated localization of ncMTOCs to the cortex is essential for proper MT network organization, and possibly minus-end stabilization as suggested in several studies (Feng et al., 2019, Goodwin and Vale, 2011, Nashchekin et al., 2016).

Altogether, we now propose an integrated model in which MT reduction and disorganization may result from multiple complementary mechanisms operating downstream of Kinesin-1/Ensconsin loss. While some aspects remain difficult to test directly in our in vivo system, the convergence of our data with recent mechanistic studies provides an interesting conceptual framework. The Discussion has been revised to reflect this comprehensive view in a dedicated paragraph (“A possible regulation of MT dynamics in the oocyte at both plus end minus MT ends by Ens and Khc” lane 415-432).

4) The Shot overexpression experiments presented in Fig.3 E-F, Fig.4D and TableS1 are very confusing. Originally , the authors used Shot-GFP overexpression at stage 9 to show that there is a decrease of ncMTOCs at the cortex in ens mutants (Fig.3 E-F) and speculated that this caused the defects in MT length and cytoplasmic advection at stage 10B. However the authors later state on page 8 that : "Shot overexpression (Shot OE) was sufficient to rescue the presence of long cortical MTs and ooplasmic advection in most ens oocytes (9/14), resembling the patterns observed in controls (Figures 4B right panel and 4D). Moreover, while ens females were fully sterile, overexpression of Shot was sufficient to restore that loss of fertility (Table S1)". Is this the same UAS Shot-GFP and VP16 Gal4 used in both experiments? If so, this contradictions puts the authors conclusions in question.

This is an important point that requires clarification regarding our experimental design.

The Shot-YFP construct is a genomic insertion on chromosome 3. The ens mutation is also located on chromosome 3 and we were unable to recombine this transgene with the ens mutant for live quantification of cortical Shot. To circumvent this technical limitation, we used a UAS-Shot.L(C)-GFP transgenic construct driven by a maternal driver, expressed in both wild-type (control) and ens mutant oocytes. We validated that the expression level and subcellular localization of UAS-Shot.L(C)-GFP were comparable to those of the genomic Shot-YFP (new Figure S8 A and B).

From these experiments, we drew two key conclusions. First, cortical Shot.L(C)-GFP is less abundant in ens mutant oocytes compared to wild-type (the quantification has been removed from this version). Second, despite this reduced cortical accumulation, Shot.L(C)-GFP expression partially rescues ooplasmic flows and microtubule streaming in stage 10B ens mutant oocytes, and restores fertility to ens mutant females.

5) The authors based they conclusions about the involvement of Ens, Kinesin-1 and Ninein in ncMTOC anchoring on the decrease in cortical fluorescence intensity of Shot-YFP and Patronin-YFP in the corresponding mutant backgrounds. However, there is a large variation in average Shot-YFP intensity between control oocytes in different experiments. In Fig. 2F-G the average level of Shot-YFP in the control sis 130 AU while in Fig.3 G-H it is only 55 AU. This makes me worry about reliability of such measurements and the conclusions drawn from them.

To clarify this point, we have harmonized the method used to quantify the Shot-YFP signals in Figure 4E with the methodology used in Figure 3B, based on the original images. The levels are not strictly identical (Control Figure 2 B: 132.7+/-36.2 versus Control Figure 4 E: 164.0+/- 37.7). These differences are usual when experiments are performed at several-month intervals and by different users.

6) The decrease in the intensity of Shot-YFP and Patronin-YFP cortical fluorescence in ens mutant oocytes could be because of problems with ncMTOC anchoring or with ncMTOCs formation. The authors should find a way to distinguish between these two possibilities. The authors could express Ens-Mut (described in Sung et al 2008), which localises at the oocyte posterior and test whether it recruits Shot/Patronin ncMTOCs to the posterior.

We tried to obtain the fly stocks described in the 2008 paper by contacting former members of Pernille Rørth's laboratory. Unfortunately, we learned that the lab no longer exists and that all reagents, including the requested stocks, were either discarded or lost over time. To our knowledge, these materials are no longer available from any source. We regret that this limitation prevented us from performing the straightforward experiments suggested by the reviewer using these specific tools.

7) According to the Materials and Methods, the Shot-GFP used in Fig.3 E-F and Fig.4 was the BDSC line 29042. This is Shot L(C), a full-length version of Shot missing the CH1 actin-binding domain that is crucial for Shot anchoring to the cortex. If the authors indeed used this version of Shot-GFP, the interpretation of the above experiments is very difficult.

The Shot.L(C) isoform lacks the CH1 domain but retains the CH2 actin-binding motif. Truncated proteins with this domain and fused to GST retains a weak ability to bind actin in vitro. Importantly, the function of this isoform is context-dependent: it cannot rescue shot loss-of-function in neuron morphogenesis but fully restores Shot-dependent tracheal cell remodeling (Lee and Kolodziej, 2002).

In our experiments, when the Shot.L(C) isoform was expressed under the control of a maternal driver, its localization to the oocyte cortex was comparable to that of the genomic Shot-YFP construct (new Figure S8). This demonstrates unambiguously that the CH1 domain is dispensable for Shot cortical localization in oocytes, and that CH2-mediated actin binding is sufficient for this localization. Of note, a recent study showed that actin network are not equivalent highlighting the need for specific Shot isoforms harboring specialized actin-binding domain (Nashchekin et al., 2024).

We note that the expression level of Shot.L(C)-GFP in the oocyte appeared slightly lower than that of Shot-YFP (expressed under endogenous Shot regulatory sequences), as assessed by Western blot (Figure S8 A).

Critically, Shot.L(C)-GFP expression was substantially lower than that of Shot.L(A)-GFP (that harbored both the CH1 and CH2 domain). Shot.L(A)-GFP was overexpressed (Figure 8 A) and ectopically localized on MTs in both nurse cells and the ooplasm (Figure S8 B middle panel and arrow). These observations are in agreement that the Shot.L(C)-GFP rescue experiment was performed at near-physiological expression levels, strengthening the validity of our conclusions.

8) Page 6 "converted in NCs, in a region adjacent to the ring canals, Dendra-Ens-labeled MTs were found in the oocyte compartment indicating they are able to travel from NC toward the oocyte through ring canals". I have difficulty seeing the translocation of MT through the ring canals. Perhaps it would be more obvious with a movie/picture showing only one channel. Considering that f Dendra-Ens appears in the oocyte much faster than MT transport through ring canals (140nm/s, Lu et al 2022), the authors are most probably observing the translocation of free Ens rather than Ens bound to MT. The authors should also mention that Ens movement from the NC to the oocyte has been shown before with Ens MBD in Lu et al 2022 with better resolution.

We fully agree on the caveat mentioned by this reviewer: we may observe the translocation of free Dendra-Ensconsin. The experiment, was removed and replaced by referring to the work of the Gelfand lab. The movement of MTs that travel at ~140 nm/s between nurse cells toward the oocyte through the Ring Canals was reported before by Lu et al. (2022) with a very good resolution. Notably, this directional directed movement of MTs was measured using a fusion protein encompassing Ens MT-binding domain. We decided to remove this inclusive experiment and rather refer to this relevant study.

9) Page 6: The co-localization of Ninein with Ens and Shot at the oocyte cortex (Figure 2A). I have difficulty seeing this co-localisation. Perhaps it would be more obvious in merged images of only two channels and with higher resolution images

10) "a pool of the Ens-GFP co-localized with Ch-Patronin at cortical ncMTOCs at the anterior cortex (Figure 3A)". I also have difficulty seeing this.

We have performed new high-resolution acquisitions that provide clearer and more convincing evidence for the localization cortical distribution of these proteins (revised Figure 2A-2C and Figure 4A). These improved images demonstrate that Ens, Ninein, Shot, and Patronin partially colocalize at cortical ncMTOCs, as initially proposed. Importantly, the new data also reveal a spatial distinction: while Ens localizes along microtubules extending from these cortical sites, Ninein appears confined to small cytoplasmic puncta adjacent but also present on cortical microtubules.

11) "Ninein co-localizes with Ens at the oocyte cortex and partially along cortical microtubules, contributing to the maintenance of high Ens protein levels in the oocyte and its proper cortical targeting". I could not find any data showing the involvement of Ninein in the cortical targeting of Ens.

We found decreased Ens localization to MTs and to the cell cortex region (new Figure S3 A-B).

12) "our MT network analyses reveal the presence of numerous short MTs cytoplasmic clustered in an anterior pattern." "This low cortical recruitment of ncMTOCs is consistent with poor MT anchoring and their cytoplasmic accumulation." I could not find any data showing that short cortical MT observed at stage 10b in ens mutant and Khc RNAi were cytoplasmic and poorly anchored.

The sentence was removed from the revised manuscript.

13) "The egg chamber consists of interconnected cells where Dynein and Khc activities are spatially separated. Dynein facilitates transport from NCs to the oocyte, while Khc mediates both transport and advection within the oocyte." Dynein is involved in various activities in the oocyte. It anchors the oocyte nucleus and transports bcd and grk mRNA to mention a few.

The text was amended to reflect Dynein involvement in transport activities in the oocyte, with the appropriate references (lane 105-107).

14) The cartoons in Fig.2H and 3I exaggerate the effect of Ninein and Ens on cortical ncMTOCs. According to the corresponding graphs, there is a 20 and 50% decrease in each case.

New cartoons (now revised Figure 3E and 4F), are amended to reflect the ncMTOC values but also MT orientation (Figure 3E).

Significance

Given the important concerns raised, the significance of the findings is difficult to assess at this stage.

We sincerely thank the reviewer for their thorough evaluation of our manuscript. We have carefully addressed their concerns through substantial new experiments and analyses. We hope that the revised manuscript, in its current form, now provides the clarifications and additional evidence requested, and that our responses demonstrate the significance of our findings.

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

Summary: This manuscript presents an investigation into the molecular mechanisms governing spatial activation of Kinesin-1 motor protein during Drosophila oogenesis, revealing a regulatory network that controls microtubule organization and cytoplasmic transport. The authors demonstrate that Ensconsin, a MAP7 family protein and Kinesin-1 activator, is spatially enriched in the oocyte through a dual mechanism involving Dynein-mediated transport from nurse cells and cortical maintenance by Ninein. This spatial enrichment of Ens is crucial for locally relieving Kinesin-1 auto-inhibition. The Ens/Khc complex promotes cortical recruitment of non-centrosomal microtubule organizing centers (ncMTOCs), which are essential for anchoring microtubules at the cortex, enabling the formation of long, parallel microtubule streams or "twisters" that drive cytoplasmic advection during late oogenesis. This work establishes a paradigm where motor protein activation is spatially controlled through targeted localization of regulatory cofactors, with the activated motor then participating in building its own transport infrastructure through ncMTOC recruitment and microtubule network organization.

There's a lot to like about this paper! The data are generally lovely and nicely presented. The authors also use a combination of experimental approaches, combining genetics, live and fixed imaging, and protein biochemistry.

We thank the reviewer for this enthusiastic and supportive review, which helped us further strengthen the manuscript.

Concerns: Page 6: "to assay if elevation of Ninein levels was able to mis-regulate Ens localization, we overexpressed a tagged Ninein-RFP protein in the oocyte. At stage 9 the overexpressed Ninein accumulated at the anterior cortex of the oocyte and also generated large cortical aggregates able to recruit high levels of Ens (Figures 2D and 2H)... The examination of Ninein/Ens cortical aggregates obtained after Ninein overexpression showed that these aggregates were also able to recruit high levels of Patronin and Shot (Figures 2E and 2H)." Firstly, I'm not crazy about the use of "overexpressed" here, since there isn't normally any Ninein-RFP in the oocyte. In these experiments it has been therefore expressed, not overexpressed. Secondly, I don't understand what the reader is supposed to make of these data. Expression of a protein carrying a large fluorescent tag leads to large aggregates (they don't look cortical to me) that include multiple proteins - in fact, all the proteins examined. I don't understand this to be evidence of anything in particular, except that Ninein-RFP causes the accumulation of big multi-protein aggregates. While I can understand what the authors were trying to do here, I think that these data are inconclusive and should be de-emphasized.

We have revised the manuscript by replacing overexpressed with expressed (lanes 211 and 212). In addition, we now provide new localization data in both cortical (new Figure S4 A, top) and medial focal planes (new Figure S4 A, bottom), demonstrating that Ninein puncta (the word used in Rosen et al, 2019), rather than aggregates are located cortically. We also show that live IRP-labelled MTs do not colocalize with Ninein-RFP puncta. In light of the new experiments and the comments from the other reviewers, the corresponding text has been revised and de-emphasized accordingly.

Page 7: "Co-immunoprecipitations experiments revealed that Patronin was associated with Shot-YFP, as shown previously (Nashchekin et al., 2016), but also with EnsWT-GFP, indicating that Ens, Shot and Patronin are present in the same complex (Figure 3B)." I do not agree that association between Ens-GFP and Patronin indicates that Ens is in the same complex as Shot and Patronin. It is also very possible that there are two (or more) distinct protein complexes. This conclusion could therefore be softened. Instead of "indicating" I suggest "suggesting the possibility."

We have toned down this conclusion and indicated “suggesting the possibility” (lane 238-239).

Page 7: "During stage 9, the average subcortical MT length, taken at one focal plane in live oocytes (see methods)..." I appreciate that the authors have been careful to describe how they measured MT length, as this is a major point for interpretation. I think the reader would benefit from an explanation of why they decided to measure in only one focal plane and how that decision could impact the results.

We appreciate this helpful suggestion. Cortical microtubules are indeed highly dynamic and extend in multiple directions, including along the Z-axis. Moreover, their diameter is extremely small (approximately 25 nm), making it technically challenging to accurately measure their full length with high resolution using our Zeiss Airyscan confocal microscope (over several, microns): the acquisition of Z-stacks is relatively slow and therefore not well suited to capturing the rapid dynamics of these microtubules. Consequently, our length measurements represent a compromise and most likely underestimate the actual lengths of microtubules growing outside the focal plane. We note that other groups have encountered similar technical limitations (Parton et al., 2011).

Page 7: "... the MTs exhibited an orthogonal orientation relative to the anterior cortex (Figures 4A left panels, 4C and 4E)." This phenotype might not be obvious to readers. Can it be quantified?

We have now analyzed the orientation of microtubules (MTs) along the dorso-ventral axis. Our analysis shows that ens, Khc RNAi oocytes (new Figure 5B), and, to a lesser extent, Nin mutant oocytes (new Figure 3D), display a more random MT orientation compared to wild-type (WT) oocytes. In WT oocytes, MTs are predominantly oriented toward the posterior pole, consistent with previous findings (Parton et al., 2011).

Page 8: "Altogether, the analyses of Ens and Khc defective oocytes suggested that MT organization defects during late oogenesis (stage 10B) were caused by an initial failure of ncMTOCs to reach the cell cortex. Therefore, we hypothesized that overexpression of the ncMTOC component Shot could restore certain aspects of microtubule cortical organization in ens-deficient oocytes. Indeed, Shot overexpression (Shot OE) was sufficient to rescue the presence of long cortical MTs and ooplasmic advection in most ens oocytes (9/14)..." The data are clear, but the explanation is not. Can the authors please explain why adding in more of an ncMTOC component (Shot) rescues a defect of ncMTOC cortical localization?

We propose that cytoplasmic ncMTOCs can bind the cell cortex via the Shot subunit that is so far the only component that harbors actin-binding motifs. Therefore, we propose that elevating cytoplasmic Shot increase the possibility of Shot to encounter the cortex by diffusion when flows are absent. This is now explained lane 282-285.

I'm grateful to the authors for their inclusion of helpful diagrams, as in Figures 1G and 2H. I think the manuscript might benefit from one more of these at the end, illustrating the ultimate model.

We have carefully considered and followed the reviewer’s suggestions. In response, we have included a new figure illustrating our proposed model: the recruitment of ncMTOCs to the cell cortex through low Khc-mediated flows at stage 9 enhances cortical microtubule density, which in turn promotes self-amplifying flows (new Figure 7, panels A to C). Note that this Figure also depicts activation of Khc by loss of auto-inhibition (Figure 7, panel D).

I'm sorry to say that the language could use quite a bit of polishing. There are missing and extraneous commas. There is also regular confusion between the use of plural and singular nouns. Some early instances include:

1. Page 3: thought instead of "thoughted."
2. Page 5: "A previous studies have revealed"
3. Page 5: "A significantly loss"
4. Page 6: "troughs ring canals" should be "through ring canals"
5. Page 7: lives stage 9 oocytes
6. Page 7: As ens and Khc RNAi oocytes exhibits
7. Page 7: we examined in details
8. Page 7: This average MT length was similar in Khc RNAi and ens mutant oocyte..

We apologize for errors. We made the appropriate corrections of the manuscript.

Reviewer #4 (Significance (Required)):

This work makes a nice conceptual advance by showing that motor activation controls its own transport infrastructure, a paradigm that could extend to other systems requiring spatially regulated transport.

We thank the reviewers for their evaluation of the manuscript and helpful comments.

Author response:

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

Reviewer #1 (Public review):

Summary:

This paper presents two experiments, both of which use a target detection paradigm to investigate the speed of statistical learning. The first experiment is a replication of Batterink, 2017, in which participants are presented with streams of uniform-length, trisyllabic nonsense words and asked to detect a target syllable. The results replicate previous findings, showing that learning (in the form of response time facilitation to later-occurring syllables within a nonsense word) occurs after a single exposure to a word. In the second experiment, participants are presented with streams of variable-length nonsense words (two trisyllabic words and two disyllabic words) and perform the same task. A similar facilitation effect was observed as in Experiment 1. The authors interpret these findings as evidence that target detection requires mechanisms different from segmentation. They present results of a computational model to simulate results from the target detection task and find that an "anticipation mechanism" can produce facilitation effects, without performing segmentation. The authors conclude that the mechanisms involved in the target detection task are different from those involved in the word segmentation task.

Strengths:

The paper presents multiple experiments that provide internal replication of a key experimental finding, in which response times are facilitated after a single exposure to an embedded pseudoword. Both experimental data and results from a computational model are presented, providing converging approaches for understanding and interpreting the main results. The data are analyzed very thoroughly using mixed effects models with multiple explanatory factors.

Weaknesses:

In my view, the main weaknesses of this study relate to the theoretical interpretation of the results.

(1) The key conclusion from these findings is that the facilitation effect observed in the target detection paradigm is driven by a different mechanism (or mechanisms) than those involved in word segmentation. The argument here I think is somewhat unclear and weak, for several reasons:

First, there appears to be some blurring in what exactly is meant by the term "segmentation" with some confusion between segmentation as a concept and segmentation as a paradigm.

Conceptually, segmentation refers to the segmenting of continuous speech into words. However, this conceptual understanding of segmentation (as a theoretical mechanism) is not necessarily what is directly measured by "traditional" studies of statistical learning, which typically (at least in adults) involve exposure to a continuous speech stream followed by a forced-choice recognition task of words versus recombined foil items (part-words or nonwords). To take the example provided by the authors, a participant presented with the sequence GHIABCDEFABCGHI may endorse ABC as being more familiar than BCG, because ABC is presented more frequently together and the learned association between A and B is stronger than between C and G. However, endorsement of ABC over BCG does not necessarily mean that the participant has "segmented" ABC from the speech stream, just as faster reaction times in responding to syllable C versus A do not necessarily indicate successful segmentation. As the authors argue on page 7, "an encounter to a sequence in which two elements co-occur (say, AB) would theoretically allow the learner to use the predictive relationship during a subsequent encounter (that A predicts B)." By the same logic, encoding the relationship between A and B could also allow for the above-chance endorsement of items that contain AB over items containing a weaker relationship.

Both recognition performance and facilitation through target detection reflect different outcomes of statistical learning. While they may reflect different aspects of the learning process and/or dissociable forms of memory, they may best be viewed as measures of statistical learning, rather than mechanisms in and of themselves.

Thanks for this nuanced discussion, and this is an important point that R2 also raised. We agree that segmentation can refer to both an experimental paradigm and a mechanism that accounts for learning in the experimental paradigm. In the experimental paradigm, participants are asked to identify which words they believe to be (whole) words from the continuous syllable stream. In the target-detection experimental paradigm, participants are not asked to identify words from continuous streams, and instead, they respond to the occurrences of a certain syllable. It’s possible that learners employ one mechanism in these two tasks, or that they employ separate mechanisms. It’s also the case that, if all we have is positive evidence for both experimental paradigms, i.e., learners can succeed in segmentation tasks as well as in target detection tasks with different types of sequences, we would have no way of talking about different mechanisms, as you correctly suggested that evidence for segmenting AB and processing B faster following A, is not evidence for different mechanisms.

However, that is not the case. When the syllable sequences contain same-length subsequences (i.e., words), learning is indeed successful in both segmentation and target detection tasks. However, in studies such as Hoch et al. (2013), findings suggest that words from mixed-length sequences are harder to segment than words from uniform-length sequences. This finding exists in adult work (e.g., Hoch et al. 2013) as well as infant work (Johnson & Tyler, 2010), and replicated here in the newly included Experiment 3, which stands in contrast to the positive findings of the facilitation effect with mixed-length sequences in the target detection paradigm (one of our main findings in the paper). Thus, it seems to be difficult to explain, if the learning mechanisms were to be the same, why humans can succeed in mixed-length sequences in target detection (as shown in Experiment 2) but fail in uniform-length sequences (as shown in Hoch et al. and Experiment 3).

In our paper, we have clarified these points describe the separate mechanisms in more detail, in both the Introduction and General Discussion sections.

(2) The key manipulation between experiments 1 and 2 is the length of the words in the syllable sequences, with words either constant in length (experiment 1) or mixed in length (experiment 2). The authors show that similar facilitation levels are observed across this manipulation in the current experiments. By contrast, they argue that previous findings have found that performance is impaired for mixed-length conditions compared to fixed-length conditions. Thus, a central aspect of the theoretical interpretation of the results rests on prior evidence suggesting that statistical learning is impaired in mixed-length conditions. However, it is not clear how strong this prior evidence is. There is only one published paper cited by the authors - the paper by Hoch and colleagues - that supports this conclusion in adults (other mentioned studies are all in infants, which use very different measures of learning). Other papers not cited by the authors do suggest that statistical learning can occur to stimuli of mixed lengths (Thiessen et al., 2005, using infant-directed speech; Frank et al., 2010 in adults). I think this theoretical argument would be much stronger if the dissociation between recognition and facilitation through RTs as a function of word length variability was demonstrated within the same experiment and ideally within the same group of participants.

To summarize the evidence of learning uniform-length and mixed-length sequences (which we discussed in the Introduction section), “even though infants and adults alike have shown success segmenting syllable sequences consisting of words that were uniform in length (i.e., all words were either disyllabic; Graf Estes et al., 2007; or trisyllabic, Aslin et al., 1998), both infants and adults have shown difficulty with syllable sequences consisting of words of mixed length (Johnson & Tyler, 2010; Johnson & Jusczyk, 2003a; 2003b; Hoch et al., 2013).” The newly added Experiment 3 also provided evidence for the difference in uniform-length and mixed-length sequences. Notably, we do not agree with the idea that infant work should be disregarded as evidence just because infants were tested with habituation methods; not only were the original findings (Saffran et al. 1996) based on infant work, so were many other studies on statistical learning.

There are other segmentation studies in the literature that have used mixed-length sequences, which are worth discussing. In short, these studies differ from the Saffran et al. (1996) studies in many important ways, and in our view, these differences explain why the learning was successful. Of interest, Thiessen et al. (2005) that you mentioned was based on infant work with infant methods, and demonstrated the very point we argued for: In their study, infants failed to learn when mixed-length sequences were pronounced as adult-directed speech, and succeeded in learning given infant-directed speech, which contained prosodic cues that were much more pronounced. The fact that infants failed to segment mixed-length sequences without certain prosodic cues is consistent with our claim that mixed-length sequences are difficult to segment in a segmentation paradigm. Another such study is Frank et al. (2010), where continuous sequences were presented in “sentences”. Different numbers of words were concatenated into sentences where a 500ms break was present between each sentence in the training sequence. One sentence contained only one word, or two words, and in the longest sentence, there were 24 words. The results showed that participants are sensitive to the effect of sentence boundaries, which coincide with word boundaries. In the extreme, the one-word-per-sentence condition simply presents learners with segmented word forms. In the 24-word-per-sentence condition, there are nevertheless sentence boundaries that are word boundaries, and knowing these word boundaries alone should allow learners to perform above chance in the test phase. Thus, in our view, this demonstrates that learners can use sentence boundaries to infer word boundaries, which is an interesting finding in its own right, but this does not show that a continuous syllable sequence with mixed word lengths is learnable without additional information. In summary, to our knowledge, syllable sequences containing mixed word lengths are better learned when additional cues to word boundaries are present, and there is strong evidence that syllable sequences containing uniform-word lengths are learned better than mixed-length ones.

Frank, M. C., Goldwater, S., Griffiths, T. L., & Tenenbaum, J. B. (2010). Modeling human performance in statistical word segmentation. Cognition, 117(2), 107-125.

To address your proposal of running more experiments to provide stronger evidence for our theory, we were planning to run another study to have the same group of participants do both the segmentation and target detection paradigm as suggested, but we were unable to do so as we encountered difficulties to run English-speaking participants. Instead, we have included an experiment (now Experiment 3), showing the difference between the learning of uniform-length and mixed-length sequences with the segmentation paradigm that we have never published previously. This experiment provides further evidence for adults’ difficulties in segmenting mixed-length sequences.

(3) The authors argue for an "anticipation" mechanism in explaining the facilitation effect observed in the experiments. The term anticipation would generally be understood to imply some kind of active prediction process, related to generating the representation of an upcoming stimulus prior to its occurrence. However, the computational model proposed by the authors (page 24) does not encode anything related to anticipation per se. While it demonstrates facilitation based on prior occurrences of a stimulus, that facilitation does not necessarily depend on active anticipation of the stimulus. It is not clear that it is necessary to invoke the concept of anticipation to explain the results, or indeed that there is any evidence in the current study for anticipation, as opposed to just general facilitation due to associative learning.

Thanks for raising this point. Indeed, the anticipation effect we reported is indistinguishable from the facilitation effect that we reported in the reported experiments. We have dropped this framing.

In addition, related to the model, given that only bigrams are stored in the model, could the authors clarify how the model is able to account for the additional facilitation at the 3rd position of a trigram compared to the 2nd position?

Thanks for the question. We believe it is an empirical question whether there is an additional facilitation at the 3rd position of a trigram compared to the 2nd position. To investigate this issue, we conducted the following analysis with data from Experiment 1. First, we combined the data from two conditions (exact/conceptual) from Experiment 1 so as to have better statistical power. Next, we ran a mixed effect regression with data from syllable positions 2 and 3 only (i.e., data from syllable position 1 were not included). The fixed effect included the two-way interaction between syllable position and presentation, as well as stream position, and the random effect was a by-subject random intercept and stream position as the random slope. This interaction was significant (χ²(3) =11.73, p=0.008), suggesting that there is additional facilitation to the 3rd position compared to the 2nd position.

For the model, here is an explanation of why the model assumes an additional facilitation to the 3rd position. In our model, we proposed a simple recursive relation between the RT of a syllable occurring for the nth time and the n+1^th time, which is:

and

RT(1) = RT0 + stream_pos * stream_inc, where the n in RT(n) represents the RT for the n^th presentation of the target syllable, stream_pos is the position (3-46) in the stream, and occurrence is the number of occurrences that the syllable has occurred so far in the stream.

What this means is that the model basically provides an RT value for every syllable in the stream. Thus, for a target at syllable position 1, there is a RT value as an unpredictable target, and for targets at syllable position 2, there is a facilitation effect. For targets at syllable position 3, it is facilitated the same amount. As such, there is an additional facilitation effect for syllable position 3 because effects of predication are recursive.

(4) In the discussion of transitional probabilities (page 31), the authors suggest that "a single exposure does provide information about the transitions within the single exposure, and the probability of B given A can indeed be calculated from a single occurrence of AB." Although this may be technically true in that a calculation for a single exposure is possible from this formula, it is not consistent with the conceptual framework for calculating transitional probabilities, as first introduced by Saffran and colleagues. For example, Saffran et al. (1996, Science) describe that "over a corpus of speech there are measurable statistical regularities that distinguish recurring sound sequences that comprise words from the more accidental sound sequences that occur across word boundaries. Within a language, the transitional probability from one sound to the next will generally be highest when the two sounds follow one another within a word, whereas transitional probabilities spanning a word boundary will be relatively low." This makes it clear that the computation of transitional probabilities (i.e., Y | X) is conceptualized to reflect the frequency of XY / frequency of X, over a given language inventory, not just a single pair. Phrased another way, a single exposure to pair AB would not provide a reliable estimate of the raw frequencies with which A and AB occur across a given sample of language.

Thanks for the discussion. We understand your argument, but we respectively disagree that computing transitional probabilities must be conducted under a certain theoretical framework. In our humble opinion, computing transitional probabilities is a mathematical operation, and as such, it is possible to do so with the least amount of data possible that enables the mathematical operation, which concretely is a single exposure during learning. While it is true that a single exposure may not provide a reliable estimate of frequencies or probabilities, it does provide information with which the learner can make decisions.

This is particularly true for topics under discussion regarding the minimal amount of exposure that can enable learning. It is important to distinguish the following two questions: whether learners can learn from a short exposure period (from a single exposure, in fact) and how long of an exposure period does the learner require for it to be considered to produce a reliable estimate of frequencies. Incidentally, given the fact that learners can learn from a single exposure based on Batterink (2017) and the current study, it does not appear that learners require a long exposure period to learn about transitional probabilities.

(5) In experiment 2, the authors argue that there is robust facilitation for trisyllabic and disyllabic words alike. I am not sure about the strength of the evidence for this claim, as it appears that there are some conflicting results relevant to this conclusion. Notably, in the regression model for disyllabic words, the omnibus interaction between word presentation and syllable position did not reach significance (p= 0.089). At face value, this result indicates that there was no significant facilitation for disyllabic words. The additional pairwise comparisons are thus not justified given the lack of omnibus interaction. The finding that there is no significant interaction between word presentation, word position, and word length is taken to support the idea that there is no difference between the two types of words, but could also be due to a lack of power, especially given the p-value (p = 0.010).

Thanks for the comment. Firstly, we believe there is a typo in your comment, where in the last sentence, we believe you were referring to the p-value of 0.103 (source: “The interaction was not significant (χ2(3) = 6.19, p= 0.103”). Yes, a null result with a frequentist approach cannot support a null claim, but Bayesian analyses could potentially provide evidence for the null.

To this end, we conducted a Bayes factor analysis using the approach outlined in Harms and Lakens (2018), which generates a Bayes factor by computing a Bayesian information criterion for a null model and an alternative model. The alternative model contained a three-way interaction of word length, word presentation, and word position, whereas the null model contained a two-way interaction between word presentation and word position as well as a main effect of word length. Thus, the two models only differ in terms of whether there is a three-way interaction. The Bayes factor is then computed as exp[(BICalt − BICnull)/2]. This analysis showed that there is strong evidence for the null, where the Bayes Factor was found to be exp(25.65) which is more than 1011. Thus, there is no power issue here, and there is strong evidence for the null claim that word length did not interact with other factors in Experiment 2.

There is another issue that you mentioned, of whether we should conduct pairwise comparisons if the omnibus interaction did not reach significance. This would be true given the original analysis plan, but we believe that a revised analysis plan makes more sense. In the revised analysis plan for Experiment 2, we start with the three-way interaction (as just described in the last paragraph). The three-way interaction was not significant, and after dropping the third interaction terms, the two-way interaction and the main effect of word length are both significant, and we use this as the overall model. Testing the significance of the omnibus interaction between presentation and syllable position, we found that this was significant (χ²(3) =49.77, p<0.001). This represents that, in one model, that the interaction between presentation and syllable position using data from both disyllabic and trisyllabic words. This was in addition to a significant fixed effect of word length (β=0.018, z=6.19, p<0.001). This should motivate the rest of the planned analysis, which regards pairwise comparisons in different word length conditions.

(6) The results plotted in Figure 2 seem to suggest that RTs to the first syllable of a trisyllabic item slow down with additional word presentations, while RTs to the final position speed up. If anything, in this figure, the magnitude of the effect seems to be greater for 1st syllable positions (e.g., the RT difference between presentation 1 and 4 for syllable position 1 seems to be numerically larger than for syllable position 3, Figure 2D). Thus, it was quite surprising to see in the results (p. 16) that RTs for syllable position 1 were not significantly different for presentation 1 vs. the later presentations (but that they were significant for positions 2 and 3 given the same comparison). Is this possibly a power issue? Would there be a significant slowdown to 1st syllables if results from both the exact replication and conceptual replication conditions were combined in the same analysis?

Thanks for the suggestion and your careful visual inspection of the data. After combining the data, the slowdown to 1st syllables is indeed significant. We have reported this in the results of Experiment 1 (with an acknowledgement to this review):

Results showed that later presentations took significantly longer to respond to compared to the first presentation (χ²(3) = 10.70, p=0.014), where the effect grew larger with each presentation (second presentation: β=0.011, z=1.82, p=0.069; third presentation: β=0.019, z=2.40, p=0.016; fourth presentation: β=0.034, z=3.23, p=0.001).

(7) It is difficult to evaluate the description of the PARSER simulation on page 36. Perhaps this simulation should be introduced earlier in the methods and results rather than in the discussion only.

Thanks for the suggestions. We have added two separate simulations in the paper, which should describe the PARSER simulations sufficiently, as well as provide further information on the correspondence between the simulations and the experiments. Thanks again for the great review! We believe our paper has improved significantly as a result.

Author response:

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

Reviewer #1 (Public review):

In this manuscript, Domingo et al. present a novel perturbation-based approach to experimentally modulate the dosage of genes in cell lines. Their approach is capable of gradually increasing and decreasing gene expression. The authors then use their approach to perturb three key transcription factors and measure the downstream effects on gene expression. Their analysis of the dosage response curve of downstream genes reveals marked non-linearity.

One of the strengths of this study is that many of the perturbations fall within the physiological range for each cis gene. This range is presumably between a single-copy state of heterozygous loss-of-function (log fold change of -1) and a three-copy state (log fold change of ~0.6). This is in contrast with CRISPRi or CRISPRa studies that attempt to maximize the effect of the perturbation, which may result in downstream effects that are not representative of physiological responses.

Another strength of the study is that various points along the dosage-response curve were assayed for each perturbed gene. This allowed the authors to effectively characterize the degree of linearity and monotonicity of each dosage-response relationship. Ultimately, the study revealed that many of these relationships are non-linear, and that the response to activation can be dramatically different than the response to inhibition.

To test their ability to gradually modulate dosage, the authors chose to measure three transcription factors and around 80 known downstream targets. As the authors themselves point out in their discussion about MYB, this biased sample of genes makes it unclear how this approach would generalize genome-wide. In addition, the data generated from this small sample of genes may not represent genome-wide patterns of dosage response. Nevertheless, this unique data set and approach represents a first step in understanding dosage-response relationships between genes.

Another point of general concern in such screens is the use of the immortalized K562 cell line. It is unclear how the biology of these cell lines translates to the in vivo biology of primary cells. However, the authors do follow up with cell-type-specific analyses (Figures 4B, 4C, and 5A) to draw a correspondence between their perturbation results and the relevant biology in primary cells and complex diseases.

The conclusions of the study are generally well supported with statistical analysis throughout the manuscript. As an example, the authors utilize well-known model selection methods to identify when there was evidence for non-linear dosage response relationships.

Gradual modulation of gene dosage is a useful approach to model physiological variation in dosage. Experimental perturbation screens that use CRISPR inhibition or activation often use guide RNAs targeting the transcription start site to maximize their effect on gene expression. Generating a physiological range of variation will allow others to better model physiological conditions.

There is broad interest in the field to identify gene regulatory networks using experimental perturbation approaches. The data from this study provides a good resource for such analytical approaches, especially since both inhibition and activation were tested. In addition, these data provide a nuanced, continuous representation of the relationship between effectors and downstream targets, which may play a role in the development of more rigorous regulatory networks.

Human geneticists often focus on loss-of-function variants, which represent natural knock-down experiments, to determine the role of a gene in the biology of a trait. This study demonstrates that dosage response relationships are often non-linear, meaning that the effect of a loss-of-function variant may not necessarily carry information about increases in gene dosage. For the field, this implies that others should continue to focus on both inhibition and activation to fully characterize the relationship between gene and trait.

We thank the reviewer for their thoughtful and thorough evaluation of our study. We appreciate their recognition of the strengths of our approach, particularly the ability to modulate gene dosage within a physiological range and to capture non-linear dosage-response relationships. We also agree with the reviewer’s points regarding the limitations of gene selection and the use of K562 cells, and we are encouraged that the reviewer found our follow-up analyses and statistical framework to be well-supported. We believe this work provides a valuable foundation for future genome-wide applications and more physiologically relevant perturbation studies.

Reviewer #2 (Public review):

Summary:

This work investigates transcriptional responses to varying levels of transcription factors (TFs). The authors aim for gradual up- and down-regulation of three transcription factors GFI1B, NFE2, and MYB in K562 cells, by using a CRISPRa- and a CRISPRi line, together with sgRNAs of varying potency. Targeted single-cell RNA sequencing is then used to measure gene expression of a set of 90 genes, which were previously shown to be downstream of GFI1B and NFE2 regulation. This is followed by an extensive computational analysis of the scRNA-seq dataset. By grouping cells with the same perturbations, the authors can obtain groups of cells with varying average TF expression levels. The achieved perturbations are generally subtle, not reaching half or double doses for most samples, and up-regulation is generally weak below 1.5-fold in most cases. Even in this small range, many target genes exhibit a non-linear response. Since this is rather unexpected, it is crucial to rule out technical reasons for these observations.

We thank the reviewer for their detailed and thoughtful assessment of our work. We are encouraged by their recognition of the strengths of our study, including the value of quantitative CRISPR-based perturbation coupled with single-cell transcriptomics, and its potential to inform gene regulatory network inference. Below, we address each of the concerns raised:

Strengths:

The work showcases how a single dataset of CRISPRi/a perturbations with scRNA-seq readout and an extended computational analysis can be used to estimate transcriptome dose responses, a general approach that likely can be built upon in the future.

Weaknesses:

(1) The experiment was only performed in a single replicate. In the absence of an independent validation of the main findings, the robustness of the observations remains unclear.

We acknowledge that our study was performed in a single pooled experiment. While additional replicates would certainly strengthen the findings, in high-throughput single-cell CRISPR screens, individual cells with the same perturbation serve as effective internal replicates. This is a common practice in the field. Nevertheless, we agree that biological replicates would help control for broader technical or environmental effects.

(2) The analysis is based on the calculation of log-fold changes between groups of single cells with non-targeting controls and those carrying a guide RNA driving a specific knockdown. How the fold changes were calculated exactly remains unclear, since it is only stated that the FindMarkers function from the Seurat package was used, which is likely not optimal for quantitative estimates. Furthermore, differential gene expression analysis of scRNA-seq data can suffer from data distortion and mis-estimations (Heumos et al. 2023 (https://doi.org/10.1038/s41576-023-00586-w), Nguyen et al. 2023 (https://doi.org/10.1038/s41467-023-37126-3)). In general, the pseudo-bulk approach used is suitable, but the correct treatment of drop-outs in the scRNA-seq analysis is essential.

We thank the reviewer for highlighting recent concerns in the field. A study benchmarking association testing methods for perturb-seq data found that among existing methods, Seurat’s FindMarkers function performed the best (T. Barry et al. 2024).

In the revised Methods, we now specify the formula used to calculate fold change and clarify that the estimates are derived from the Wilcoxon test implemented in Seurat’s FindMarkers function. We also employed pseudo-bulk grouping to mitigate single-cell noise and dropout effects.

(3) Two different cell lines are used to construct dose-response curves, where a CRISPRi line allows gene down-regulation and the CRISPRa line allows gene upregulation. Although both lines are derived from the same parental line (K562) the expression analysis of Tet2, which is absent in the CRISPRi line, but expressed in the CRISPRa line (Figure S3A) suggests substantial clonal differences between the two lines. Similarly, the PCA in S4A suggests strong batch effects between the two lines. These might confound this analysis.

We agree that baseline differences between CRISPRi and CRISPRa lines could introduce confounding effects if not appropriately controlled for. We emphasize that all comparisons are made as fold changes relative to non-targeting control (NTC) cells within each line, thereby controlling for batch- and clone-specific baseline expression. See figures S4A and S4B.

(4) The study uses pseudo-bulk analysis to estimate the relationship between TF dose and target gene expression. This requires a system that allows quantitative changes in TF expression. The data provided does not convincingly show that this condition is met, which however is an essential prerequisite for the presented conclusions. Specifically, the data shown in Figure S3A shows that upon stronger knock-down, a subpopulation of cells appears, where the targeted TF is not detected anymore (drop-outs). Also Figure 3B (top) suggests that the knock-down is either subtle (similar to NTCs) or strong, but intermediate knock-down (log2-FC of 0.5-1) does not occur. Although the authors argue that this is a technical effect of the scRNA-seq protocol, it is also possible that this represents a binary behavior of the CRISPRi system. Previous work has shown that CRISPRi systems with the KRAB domain largely result in binary repression and not in gradual down-regulation as suggested in this study (Bintu et al. 2016 (https://doi.org/10.1126/science.aab2956), Noviello et al. 2023 (https://doi.org/10.1038/s41467-023-38909-4)).

Figure S3A shows normalized expression values, not fold changes. A pseudobulk approach reduces single-cell noise and dropout effects. To test whether dropout events reflect true binary repression or technical effects, we compared trans-effects across cells with zero versus low-but-detectable target gene expression (Figure S3B). These effects were highly concordant, supporting the interpretation that dropout is largely technical in origin. We agree that KRAB-based repression can exhibit binary behavior in some contexts, but our data suggest that cells with intermediate repression exist and are biologically meaningful. In ongoing unpublished work, we pursue further analysis of these data at the single cell level, and show that for nearly all guides the dosage effects are indeed gradual rather than driven by binary effects across cells.

(5) One of the major conclusions of the study is that non-linear behavior is common. This is not surprising for gene up-regulation, since gene expression will reach a plateau at some point, but it is surprising to be observed for many genes upon TF down-regulation. Specifically, here the target gene responds to a small reduction of TF dose but shows the same response to a stronger knock-down. It would be essential to show that his observation does not arise from the technical concerns described in the previous point and it would require independent experimental validations.

This phenomenon—where relatively small changes in cis gene dosage can exceed the magnitude of cis gene perturbations—is not unique to our study. This also makes biological sense, since transcription factors are known to be highly dosage sensitive and generally show a smaller range of variation than many other genes (that are regulated by TFs). Empirically, these effects have been observed in previous CRISPR perturbation screens conducted in K562 cells, including those by Morris et al. (2023), Gasperini et al. (2019), and Replogle et al. (2022), to name but a few studies that our lab has personally examined the data of.

(6) One of the conclusions of the study is that guide tiling is superior to other methods such as sgRNA mismatches. However, the comparison is unfair, since different numbers of guides are used in the different approaches. Relatedly, the authors point out that tiling sometimes surpassed the effects of TSS-targeting sgRNAs, however, this was the least fair comparison (2 TSS vs 10 tiling guides) and additionally depends on the accurate annotation of TSS in the relevant cell line.

We do not draw this conclusion simply from observing the range achieved but from a more holistic observation. We would like to clarify that the number of sgRNAs used in each approach is proportional to the number of base pairs that can be targeted in each region: while the TSS-targeting strategy is typically constrained to a small window of a few dozen base pairs, tiling covers multiple kilobases upstream and downstream, resulting in more guides by design rather than by experimental bias. The guides with mismatches do not have a great performance for gradual upregulation.

We would also like to point out that the observation that the strongest effects can arise from regions outside the annotated TSS is not unique to our study and has been demonstrated in prior work (referenced in the text).

To address this concern, we have revised the text to clarify that we do not consider guide tiling to be inherently superior to other approaches such as sgRNA mismatches. Rather, we now describe tiling as a practical and straightforward strategy to obtain a wide range of gene dosage effects without requiring prior knowledge beyond the approximate location of the TSS. We believe this rephrasing more accurately reflects the intent and scope of our comparison.

(7) Did the authors achieve their aims? Do the results support the conclusions?: Some of the most important conclusions are not well supported because they rely on accurately determining the quantitative responses of trans genes, which suffers from the previously mentioned concerns.

We appreciate the reviewer’s concern, but we would have wished for a more detailed characterization of which conclusions are not supported, given that we believe our approach actually accounts for the major concerns raised above. We believe that the observation of non-linear effects is a robust conclusion that is also consistent with known biology, with this paper introducing new ways to analyze this phenomenon.

(8) Discussion of the likely impact of the work on the field, and the utility of the methods and data to the community:

Together with other recent publications, this work emphasizes the need to study transcription factor function with quantitative perturbations. Missing documentation of the computational code repository reduces the utility of the methods and data significantly.

Documentation is included as inline comments within the R code files to guide users through the analysis workflow.

Reviewer #1 (Recommendations for the authors):

In Figure 3C (and similar plots of dosage response curves throughout the manuscript), we initially misinterpreted the plots because we assumed that the zero log fold change on the horizontal axis was in the middle of the plot. This gives the incorrect interpretation that the trans genes are insensitive to loss of GFI1B in Figure 3C, for instance. We think it may be helpful to add a line to mark the zero log fold change point, as was done in Figure 3A.

We thank the reviewer for this helpful suggestion. To improve clarity, we have added a vertical line marking the zero log fold change point in Figure 3C and all similar dosage-response plots. We agree this makes the plots easier to interpret at a glance.

Similarly, for heatmaps in the style of Figure 3B, it may be nice to have a column for the non-targeting controls, which should be a white column between the perturbations that increase versus decrease GFI1B.

We appreciate the suggestion. However, because all perturbation effects are computed relative to the non-targeting control (NTC) cells, explicitly including a separate column for NTC in the heatmap would add limited interpretive value and could unnecessarily clutter the figure. For clarity, we have emphasized in the figure legend that the fold changes are relative to the NTC baseline.

We found it challenging to assess the degree of uncertainty in the estimation of log fold changes throughout the paper. For example, the authors state the following on line 190: "We observed substantial differences in the effects of the same guide on the CRISPRi and CRISPRa backgrounds, with no significant correlation between cis gene fold-changes." This claim was challenging to assess because there are no horizontal or vertical error bars on any of the points in Figure 2A. If the log fold change estimates are very noisy, the data could be consistent with noisy observations of a correlated underlying process. Similarly, to our understanding, the dosage response curves are fit assuming that the cis log fold changes are fixed. If there is excessive noise in the estimation of these log fold changes, it may bias the estimated curves. It may be helpful to give an idea of the amount of estimation error in the cis log fold changes.

We agree that assessing the uncertainty in log fold change estimates is important for interpreting both the lack of correlation between CRISPRi and CRISPRa effects (Figure 2A) and the robustness of the dosage-response modeling.

In response, we have now updated Figure 2A to include both vertical and horizontal error bars, representing the standard errors of the log2 fold-change estimates for each guide in the CRISPRi and CRISPRa conditions. These error estimates were computed based on the differential expression analysis performed using the FindMarkers function in Seurat, which models gene expression differences between perturbed and control cells. We also now clarify this in the figure legend and methods.

The authors mention hierarchical clustering on line 313, which identified six clusters. Although a dendrogram is provided, these clusters are not displayed in Figure 4A. We recommend displaying these clusters alongside the dendrogram.

We have added colored bars indicating the clusters to improve the clarity. Thank you for the suggestion.

In Figures 4B and 4C, it was not immediately clear what some of the gene annotations meant. For example, neither the text nor the figure legend discusses what "WBCs", "Platelets", "RBCs", or "Reticulocytes" mean. It would be helpful to include this somewhere other than only the methods to make the figure more clear.

To improve clarity, we have updated the figure legends for Figures 4B and 4C to explicitly define these abbreviations.

We struggled to interpret Figure 4E. Although the authors focus on the association of MYB with pHaplo, we would have appreciated some general discussion about the pattern of associations seen in the figure and what the authors expected to observe.

We have changed the paragraph to add more exposition and clarification:

“The link between selective constraint and response properties is most apparent in the MYB trans network. Specifically, the probability of haploinsufficiency (pHaplo) shows a significant negative correlation with the dynamic range of transcriptional responses (Figure 4G): genes under stronger constraint (higher pHaplo) display smaller dynamic ranges, indicating that dosage-sensitive genes are more tightly buffered against changes in MYB levels. This pattern was not reproduced in the other trans networks (Figure 4E)”.

Line 71: potentially incorrect use of "rending" and incorrect sentence grammar.

Fixed

Line 123: "co-expression correlation across co-expression clusters" - authors may not have intended to use "co-expression" twice.

Original sentence was correct.

Line 246: "correlations" is used twice in "correlations gene-specific correlations."

Fixed.

Reviewer #2 (Recommendations for the authors):

(1) To show that the approach indeed allows gradual down-regulation it would be important to quantify the know-down strength with a single-cell readout for a subset of sgRNAs individually (e.g. flowfish/protein staining flow cytometry).

We agree that single-cell validation of knockdown strength using orthogonal approaches such as flowFISH or protein staining would provide additional support. However, such experiments fall outside the scope of the current study and are not feasible at this stage. We note that the observed transcriptomic changes and dosage responses across multiple perturbations are consistent with effective and graded modulation of gene expression.

(2) Similarly, an independent validation of the observed dose-response relationships, e.g. with individual sgRNAs, can be helpful to support the conclusions about non-linear responses.

Fig. S4C includes replication of trans-effects for a handful of guides used both in this study and in Morris et al. While further orthogonal validation of dose-response relationships would be valuable, such extensive additional work is not currently feasible within the scope of this study. Nonetheless, the high degree of replication in Fig. S4C as well as consistency of patterns observed across multiple sgRNAs and target genes provides strong support for the conclusions drawn from our high-throughput screen.

(3) The calculation of the log2 fold changes should be documented more precisely. To perform a pseudo-bulk analysis, the raw UMI counts should be summed up in each group (NTC, individual targeting sgRNAs), including zero counts, then the data should be normalized and the fold change should be calculated. The DESeq package for example would be useful here.

We have updated the methods in the manuscript to provide more exposition of how the logFC was calculated:

“In our differential expression (DE) analysis, we used Seurat’s FindMarkers() function, which computes the log fold change as the difference between the average normalized gene expression in each group on the natural log scale:

Logfc = log_e(mean(expression in group 1)) - log_e(mean(expression in group 2))

This is calculated in pseudobulk where cells with the same sgRNA are grouped together and the mean expression is compared to the mean expression of cells harbouring NTC guides. To calculate per-gene differential expression p-value between the two cell groups (cells with sgRNA vs cells with NTC), Wilcoxon Rank-Sum test was used”.

(4) A more careful characterization of the cell lines used would be helpful. First, it would be useful to include the quality controls performed when the clonal lines were selected, in the manuscript. Moreover, a transcriptome analysis in comparison to the parental cell line could be performed to show that the cell lines are comparable. In addition, it could be helpful to perform the analysis of the samples separately to see how many of the response behaviors would still be observed.

Details of the quality control steps used during the selection of the CRISPRa clonal line are already included in the Methods section, and Fig. S4A shows the transcriptome comparison of CRISPRi and CRISPRa lines also for non-targeting guides. Regarding the transcriptomic comparison with the parental cell line, we agree that such an analysis would be informative; however, this would require additional experiments that are not feasible within the scope of the current study. Finally, while analyzing the samples separately could provide further insight into response heterogeneity, we focused on identifying robust patterns across perturbations that are reproducible in our pooled screening framework. We believe these aggregate analyses capture the major response behaviors and support the conclusions drawn.

(5) In general we were surprised to see such strong responses in some of the trans genes, in some cases exceeding the fold changes of the cis gene perturbation more than 2x, even at the relatively modest cis gene perturbations (Figures S5-S8). How can this be explained?

This phenomenon—where trans gene responses can exceed the magnitude of cis gene perturbations—is not unique to our study. Similar effects have been observed in previous CRISPR perturbation screens conducted in K562 cells, including those by Morris et al. (2023), Gasperini et al. (2019), and Replogle et al. (2022).

Several factors may contribute to this pattern. One possibility is that certain trans genes are highly sensitive to transcription factor dosage, and therefore exhibit amplified expression changes in response to relatively modest upstream perturbations. Transcription factors are known to be highly dosage sensitive and generally show a smaller range of variation than many other genes (that are regulated by TFs). Mechanistically, this may involve non-linear signal propagation through regulatory networks, in which intermediate regulators or feedback loops amplify the downstream transcriptional response. While our dataset cannot fully disentangle these indirect effects, the consistency of this observation across multiple studies suggests it is a common feature of transcriptional regulation in K562 cells.

(6) In the analysis shown in Figure S3B, the correlation between cells with zero count and >0 counts for the cis gene is calculated. For comparison, this analysis should also show the correlation between the cells with similar cis-gene expression and between truly different populations (e.g. NTC vs strong sgRNA).

The intent of Figure S3B was not to compare biologically distinct populations or perform differential expression analyses—which we have already conducted and reported elsewhere in the manuscript—but rather to assess whether fold change estimates could be biased by differences in the baseline expression of the target gene across individual cells. Specifically, we sought to determine whether cells with zero versus non-zero expression (as can result from dropouts or binary on/off repression from the KRAB-based CRISPRi system) exhibit systematic differences that could distort fold change estimation. As such, the comparisons suggested by the reviewer do not directly relate to the goal of the analysis which Figure S3B was intended to show.

(7) It is unclear why the correlation between different lanes is assessed as quality control metrics in Figure S1C. This does not substitute for replicates.

The intent of Figure S1C was not to serve as a general quality control metric, but rather to illustrate that the targeted transcript capture approach yielded consistent and specific signal across lanes. We acknowledge that this may have been unclear and have revised the relevant sentence in the text to avoid misinterpretation.

“We used the protein hashes and the dCas9 cDNA (indicating the presence or absence of the KRAB domain) to demultiplex and determine the cell line—CRISPRi or CRISPRa. Cells containing a single sgRNA were identified using a Gaussian mixture model (see Methods). Standard quality control procedures were applied to the scRNA-seq data (see Methods). To confirm that the targeted transcript capture approach worked as intended, we assessed concordance across capture lanes (Figure S1C)”.

(8) Figures and legends often miss important information. Figure 3B and S5-S8: what do the transparent bars represent? Figure S1A: color bar label missing. Figure S4D: what are the lines?, Figure S9A: what is the red line? In Figure S8 some of the fitted curves do not overlap with the data points, e.g. PKM. Fig. 2C: why are there more than 96 guide RNAs (see y-axis)?

We have addressed each point as follows:

Figure 3B: The figure legend has been updated to clarify the meaning of the transparent bars.

Figures S5–S8: There are no transparent bars in these figures; we confirmed this in the source plots.

Figure S1A: The color bar label is already described in the figure legend, but we have reformulated the caption text to make this clearer.

Figure S4D: The dashed line represents a linear regression between the x and y variables. The figure caption has been updated accordingly.

Figure S9A: We clarified that the red line shows the median ∆AIC across all genes and conditions.

Figure S8: We agree that some fitted curves (e.g., PKM) do not closely follow the data points. This reflects high noise in these specific measurements; as noted in the text, TET2 is not expected to exert strong trans effects in this context.

Figure 2C: Thank you for catching this. The y-axis numbers were incorrect because the figure displays the proportion of guides (summing to 100%), not raw counts. We have corrected the y-axis label and updated the numbers in the figure to resolve this inconsistency.

(9) The code is deposited on Github, but documentation is missing.

Documentation is included as inline comments within the R code files to guide users through the analysis workflow.

(10) The methods miss a list of sgRNA target sequences.

We thank the reviewer for this observation. A complete table containing all processed data, including the sequences of the sgRNAs used in this study, is available at the following GEO link:

https://www.ncbi.nlm.nih.gov/geo/download/?acc=GSE257547&format=file&file=GSE257547%5Fd2n%5Fprocessed%5Fdata%2Etxt%2Egz

(11) In some parts, the language could be more specific and/or the readability improved, for example:

Line 88: "quantitative landscape".

Changed to “quantitative patterns”.

Lines 88-91: long sentence hard to read.

This complex sentence was broken up into two simpler ones:

“We uncovered quantitative patterns of how gradual changes in transcription dosage lead to linear and non-linear responses in downstream genes. Many downstream genes are associated with rare and complex diseases, with potential effects on cellular phenotypes”.

Line 110: "tiling sgRNAs +/- 1000 bp from the TSS", could maybe be specified by adding that the average distance was around 100 or 110 bps?

Lines 244-246: hard to understand.

We struggle to see the issue here and are not sure how it can be reworded.

Lines 339-342: hard to understand.

These sentences have been reworded to provide more clarity.

(12) A number of typos, and errors are found in the manuscript:

Line 71: "SOX2" -> "SOX9".

FIXED

Line 73: "rending" -> maybe "raising" or "posing"?

FIXED

Line 157: "biassed".

FIXED

Line 245: "exhibited correlations gene-specific correlations with".

FIXED

Multiple instances, e.g. 261: "transgene" -> "trans gene".

FIXED

Line 332: "not reproduced with among the other".

FIXED

Figure S11: betweenness.

This is the correct spelling

There are more typos that we didn't list here.

We went through the manuscript and corrected all the spelling errors and typos.

its hard to escape racism in writing education. Teachers can use existing scholarship to learn how to teach fairly.

Different ways to use a formal and informal standard English.

While reading this article, I thought of those moments when people said "just kidding", but for children, it was not just a joke. Adults might find pranks amusing, but the fear and humiliation children feel at that moment are one hundred percent real. Especially when they are recorded by cameras, posted online, and shown to strangers as a joke, that sense of powerlessness may linger in their hearts for a long time. Children cannot understand that "this is entertainment", they only think that if even their parents can laugh at them, then who else can they trust? This made me realize that laughter and hurt are sometimes separated by only a very thin line, and we often cross it when children are at their most vulnerable.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Revision Plan

Manuscript number: RC-2025-03208

Corresponding author(s): Jared Nordman

[The "revision plan" should delineate the revisions that authors intend to carry out in response to the points raised by the referees. It also provides the authors with the opportunity to explain their view of the paper and of the referee reports.

• *

The document is important for the editors of affiliate journals when they make a first decision on the transferred manuscript. It will also be useful to readers of the reprint and help them to obtain a balanced view of the paper.

• *

If you wish to submit a full revision, please use our "Full Revision" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

1. General Statements [optional]

All three reviewers of our manuscript were very positive about our work. The reviewers noted that our work represents a necessary advance that is timely, addresses important issues in the chromatin field, and will of broad interest to this community. Given the nature of our work and the positive reviews, we feel that this manuscript would best be suited for the Journal of Cell Biology.

2. Description of the planned revisions

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

Summary:

The authors investigate the function of the H3 chaperone NASP, which is known to bind directly to H3 and prevent degradation of soluble H3. What is unclear is where NASP functions in the cell (nucleus or cytoplasm), how NASP protects H3 from degradation (direct or indirect), and if NASP affects H3 dynamics (nuclear import or export). They use the powerful model system of Drosophila embryos because the soluble H3 pool is high due to maternal deposition and they make use of photoconvertable Dendra-tagged proteins, since these are maternally deposited and can be used to measure nuclear import/export rates.

Using these systems and tools, they conclude that NASP affects nuclear import, but only indirectly, because embryos from NASP mutant mothers start out with 50% of the maternally deposited H3. Because of the depleted H3 and reduced import rates, NASP deficient embryos also have reduced nucleoplasmic and chromatin-associated H3. Using a new Dendra-tagged NASP allele, the authors show that NASP and H3 have different nuclear import rates, indicating that NASP is not a chaperone that shuttles H3 into the nucleus. They test H3 levels in embryos that have no nuclei and conclude that NASP functions in the cytoplasm, and through protein aggregation assays they conclude that NASP prevents H3 aggregation.

Major comments:

The text was easy to read and logical. The data are well presented, methods are complete, and statistics are robust. The conclusions are largely reasonable. However, I am having trouble connecting the conclusions in text to the data presented in Figure 4.

First, I'm confused why the conclusion from Figure 4A is that NASP functions in the cytoplasm of the egg. Couldn't NASP be required in the ovary (in, say, nurse cell nuclei) to stimulate H3 expression and deposition into the egg? The results in 4A would look the same if the mothers deposit 50% of the normal H3 into the egg. Why is NASP functioning specifically in the cytoplasm when it is also so clearly imported into the nucleus? Maybe NASP functions wherever it is, and by preventing nuclear import, you force it to function in the cytoplasm. I do not have additional suggestions for experiments, but I think the authors need to be very clear about the different interpretations of these data and to discuss WHY they believe their conclusion is strongest.

The concern raised by the reviewer regarding NASP function during oogenesis has been addressed in a previous work published from our lab. Unfortunately, we did not do a good job conveying this work in the original version of this manuscript. We demonstrated that total H3 levels are unaffected when comparing WT and NASP mutant stage 14 egg chambers. This means that the amount of H3 deposited into the eggs does not change in the absence of NASP. To address the reviewer's comment, we will change the text to make the link to our previous work clear.

Second, an alternate conclusion from Figure 4D/E is that mothers are depositing less H3 protein into the egg, but the same total amount is being aggregated. This amount of aggregated protein remains constant in activated eggs, but additional H3 translation leads to more total H3? The authors mention that additional translation can compensate for reduced histone pools (line 416).

Similar to our response above, the total amount of H3 in wild type and NASP mutant stage 14 egg chambers is the same. Therefore, mothers are depositing equal amounts of H3 into the egg. We will make the necessary changes in the text to make this point clear.

As the function of NASP in the cytoplasm (when it clearly imports into the nucleus) and role in H3 aggregation are major conclusions of the work, the authors need to present alternative conclusions in the text or complete additional experiments to support the claims. Again, I do not have additional suggestions for experiments, but I think the authors need to be very clear about the different interpretations of these data and to discuss WHY they believe their conclusion is strongest.

A common issue raised by all three reviewers was to more convincingly demonstrate that assay that we have used to isolate protein aggregates does, in fact, isolate protein aggregates. To verify this, we will be performing the aggregate isolation assay using controls that are known to induce more protein aggregation. We will perform the aggregation assay with egg chambers or extracts that are exposed to heat shock or the aggregation-inducing chemicals Canavanine and Azetidine-2-carboxylic acid. The chemical treatment was a welcome suggestion from reviewer #3. These experiments will significantly strengthen any claims based on the outcome of the aggregation assay.

We will also make changes to the text and include other interpretations of our work as the reviewer has suggested.

Data presentation:

Overall, I suggest moving some of the supplemental figures to the main text, adding representative movie stills to show where the quantitative data originated, and moving the H3.3 data to the supplement. Not because it's not interesting, but because H3.3 and H3.2 are behaving the same.

Where possible, we will make changes to the figure display to improve the logic and flow of the manuscript

Fig 1:

It would strengthen the figure to include representative still images that led to the quantitative data, mostly so readers understand how the data were collected.

We will add representative stills to Figure 1 to help readers understand how the data is collected. We will also a representative H3-Dendra movie similar to the NASP supplemental movie.

The inclusion of a "simulated 50% H3" in panel C is confusing. Why?

We used a 50% reduction in H3 levels because that is reduction in H3 we measure in embryos laid by NASP-mutant mothers in our previous work. A reduction in H3 levels alone would be predicted to change the nuclear import rate of H3. Thus, having a quantitative model of H3 import kinetics was key in our understanding of NASP function in vivo. We will revise the text to make this clear.

I would also consider normalizing the data between A and B (and C and D) by dividing NASP/WT. This could be included in the supplement (OPTIONAL)

We can normalize the values and include the data in a supplemental figure.

Fig S1:

The data simulation S1G should be moved to the main text, since it is the primary reason the authors reject the hypothesis that NASP influences H3 import rates.

This is a good point. We will move S1G into the Figure 1.

Fig 2:

Once again, I think it would help to include a few representative images of the photoconverted Dendra2 in the main text.

We will add representative images of the photoconversion in Figure 2.

I struggled with A/B, I think due to not knowing how the data were normalized. When I realized that the WT and NASP data are not normalized to each other, but that the NASP values are likely starting less than the WT values, it made way more sense. I suggest switching the order of data presentation so that C-F are presented first to establish that there is less chromatin-bound H3 in the first place, and then present A/B to show no change in nuclear export of the H3 that is present, allowing the conclusion of both less soluble AND chromatin-bound H3.

The order of the presentation of the data was to test if NASP was acting as a nuclear receptor. Since Figure 1 compares the nuclear import, we wanted to address the nuclear export and provide a comprehensive analysis of the role of NASP in H3 nuclear dynamics before advancing on to other consequences of NASP depletion. We can add the graphs with the un-normalized values in the Supplemental Figure to show the actual difference in total intensity values.

Fig S2:

If M1-M3 indicate males, why are the ovaries also derived from males? I think this is just confusing labeling.

We will change the labelling.

Supplemental Movie S1:

Beautiful. Would help to add a time stamp (OPTIONAL).

Thank you! We will add the time stamp to the movie

Fig 3:

Panel C is the same as Fig S1A (not Fig 1A, as is said in the legend), though I appreciate the authors pointing it out in the legend. Also see line 276.

We appreciate the reviewer for pointing this out. We will make the change in the text to correct this.

Panel D is a little confusing, because presumably the "% decrease in import rate" cannot be positive (Y axis). This could be displayed as a scatter (not bar) as in Panels B/C (right) where the top of the Y axis is set to 0.

We understand the reviewer's concern that the decrease value cannot be positive. We can adjust the y-axis so that it caps off at 0.

Fig S3:

A: What do the different panels represent? I originally thought developmental time, but now I think just different representative images? Are these age-matched from time at egg lay?

The different panels show representative images. We can clarify that in the figure legend.

C: What does "embryos" mean? Same question for Fig 4A.

In this figure, embryos mean the exact number of embryos used to form the lysate for the western blot. We will clarify this in the figure legend.

Fig 4:

A: What does "embryos" mean? Number of embryos? Age in hours?

In this figure, embryos mean the exact number of embryos used to form the lysate for the western blot. We will clarify this in the figure legend.

C: Not sure the workflow figure panel is necessary, as I can't tell what each step does. This is better explained in methods. However I appreciated the short explanation in the text (lines 314-5).

The workflow panel helps to identify the samples labelled as input and aggregate for the western blot analysis. Since our input in the western blots does not refer to the total protein lysate, we feel it is helpful to point out exactly what stage at the protocol we are utilizing the sample for our analysis.

Minor comments:

The authors should describe the nature of the NASP alleles in the main text and present evidence of robust NASP depletion, potentially both in ovaries and in embryos. The antibody works well for westerns (Fig S2B). This is sort of demonstrated later in Figure 4A, but only in NAAP x twine activated eggs.

We appreciate the reviewer's comments about the NASP mutant allele. In our previous publication, we characterized the NASP mutant fly line and its effect on both stage 14 egg chambers and the embryos. We will emphasize the reference to our previous work in the text.

Lines 163, 251, 339: minor typos

Line 184: It would help to clarify- I'm assuming cytoplasmic concentration (or overall) rather than nuclear concentration. If nuclear, I'd expect the opposite relationship. This occurs again when discussing NASP (line 267). I suspect it's also not absolute concentration, but relative concentration difference between cytoplasm and nucleus. It would help clarify if the authors were more precise.

We appreciate the reviewer's point and will add the clarification in the text.

Line 189: Given that the "established integrative model" helps to reject the hypothesis that NASP is involved in H3 import, I think it's important to describe the model a little more, even though it's previously published.

We will add few sentences giving a brief description of the model to the text.

Line 203: "The measured rate of H3.2 export from the nucleus is negligible" clarify this is in WT situations and not a conclusion from this study.

We will add the clarification of this statement in the text.

Line 211: How can the authors be so sure that the decrease in WT is due to "the loss of non-chromatin bound nucleoplasmic H3.2-Dendra2?"

From the live imaging experiments, the H3.2-Dendra2 intensity in the nucleus reduces dramatically upon nuclear envelope breakdown with the only H3.2-Dendra2 intensity remaining being the chromatin bound H3.2. Excess H3.2 is imported into the nucleus and not all of it is incorporated into the chromatin. This is a unique feature of the embryo system that has been observed previously. We mention that the intensity reduction is due to the loss of non-chromatin bound nucleoplasmic H3.2.

Line 217: In the conclusion, the authors indicate that NASP indirectly affects soluble supply of H3 in the nucleoplasm. I do believe they've shown that the import rate effect is indirect, but I don't know why they conclude that the effect of NASP on the soluble nucleoplasmic H3 supply is indirect. Similarly, the conclusion is indirect on line 239. Yet, the authors have not shown it's not direct, just assumed since NASP results in 50% decrease to deposited maternal histones.

We appreciate the feedback on the conclusions of Figure 2 from the reviewer. Our conclusions are primarily based on the effect of H3 levels in the absence of NASP in the early embryos. To establish direct causal effects, it would be important to recover the phenotypes by complementation experiments and providing molecular interactions to cause the effects. In this study we have not established those specific details to make conclusions of direct effects. We will change the text to make this more clear.

Line 292: What is the nature of the NASP "mutant?" Is it a null? Similarly, what kind of "mutant" is the twine allele? Line 295.

We will include descriptions of the NASP and twine mutants in the text.

Line 316: Why did the authors use stage 14 egg chambers here when they previously used embryos? This becomes more clear later shortly, when the authors examine activated eggs, but it's confusing in text.

The reason to use stage 14 egg chambers was to establish NASP function during oogenesis. We will modify the text to emphasize the reason behind using stage 14 egg chambers.

Lines 343-348: It's unclear if the authors are drawing extended conclusions here or if they are drawing from prior literature (if so, citations would be required). For example, why during oogenesis/embryogenesis are aggregation and degradation developmentally separated?

This conclusion is based primarily based on the findings from this study (Figure 4) and out previous published work. We will modify the text for more clarity.

Lines 386-7: I do not understand why the authors conclude that H3 aggregation and degradation are "developmentally uncoupled" and why, in the absence of NASP, "H3 aggregation precedes degradation."

This is based data in Figure 4 combined with our previous working showing that the total level of H3 in not changed in NASP-mutant stage 14 egg chambers. Aggregates seem to be more persistent in the stage 14 egg chambers (oogenesis) and they get cleared out upon egg activation (entry into embryogenesis). This provides evidence for aggregation occurring prior to degradation and these two events occurring in different developmental stages. We will change the text to make this more clear.

Line 395: Why suddenly propose that NASP also functions in the nucleus to prevent aggregation, when earlier the authors suggest it functions only in the cytoplasm?

We will make the necessary edits to ensure that the results don't suggest a role of NASP exclusive to the cytoplasm. Our findings highlight a cytoplasmic function of NASP, however, we do not want to rule out that this same function couldn't occur in the nucleus.

Lines 409-413: The authors claim that histone deficiency likely does not cause the embryonic arrest seen in embryos from NASP mutant mothers. This is because H3 is reduced by 50% yet some embryos arrest long before they've depleted this supply. However, the authors also showed that H3 import rates are affected in these embryos due to lower H3 concentration. Since the early embryo cycles are so rapid, reduced H3 import rates could lead to early arrest, even though available H3 remains in the cytoplasm.

We thank the reviewer for their suggestion. This conclusion is based on the findings from the previous study from our lab which showed that the majority of the embryos laid by NASP mutant females get arrested in the very early nuclear cycles (Reviewer #1 (Significance (Required)):

The significance of the work is conceptual, as NASP is known to function in H3 availability but the precise mechanism is elusive. This work represents a necessary advance, especially to show that NASP does not affect H3 import rates, nor does it chaperone H3 into the nucleus. However, the authors acknowledge that many questions remain. Foremost, why is NASP imported into the nucleus and what is its role there?

I believe this work will be of interest to those who focus on early animal development, but NASP may also represent a tool, as the authors conclude in their discussion, to reduce histone levels during development and examine nucleosome positioning. This may be of interest to those who work on chromatin accessibility and zygotic genome activation.

I am a genetics expert who works in Drosophila embryogenesis. I do not have the expertise to evaluate the aggregate methods presented in Figure 4.

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

Summary:

This manuscript focuses on the role of the histone chaperone NASP in Drosophila. NASP is a chaperone specific to histone H3 that is conserved in mammals. Many aspects of the molecular mechanisms by which NASP selectively binds histone H3 have been revealed through biochemical studies. However, key aspects of NASP's in vivo roles remain unclear, including where in the cell NASP functions, and how it prevents H3 degradation. Through live imaging in the early Drosophila embryo, which possesses large amounts of soluble H3 protein, Das et al determine that NASP does not control nuclear import or export of H3.2 or H3.3. Instead, they find through differential centrifugation analysis that NASP functions in the cytoplasm to prevent H3 aggregation and hence its subsequent degradation.

Major Comments:

The protein aggregation assays raise several questions. From a technical standpoint, it would be helpful to have a positive control to demonstrate that the assay is effective at detecting protein aggregates. Ie. a genotype that exhibits increased protein aggregation; this could be for a protein besides H3. A common issue raised by all three reviewers was to more convincingly demonstrate that assay that we have used to isolate protein aggregates does, in fact, isolate protein aggregates. To verify this, we will be performing the aggregate isolation assay using controls that are known to induce more protein aggregation. We will perform the aggregation assay with egg chambers or extracts that are exposed to heat shock or the aggregation-inducing chemicals Canavanine and Azetidine-2-carboxylic acid. The chemical treatment was a welcome suggestion from reviewer #3. These experiments will significantly strengthen any claims based on the outcome of the aggregation assay.

If NASP is not required to prevent H3 degradation in egg chambers, then why are H3 levels much lower in NASP input lanes relative to wild-type egg chambers in Fig 4D? We appreciate the reviewer's inputs regarding the reduced H3 levels in the NASP mutant egg chambers. We observe this reduction in H3 levels in the input because of the altered solubility of H3 which leads to the loss of H3 protein at different steps of the aggregate isolation assay. We will add a supplement figure showing H3 levels at different steps of the aggregate isolation assay. We do want to stress, however, that the total levels of H3 in stage 14 egg chambers does not change between WT and the NASP mutant.

A corollary to this is that the increased fraction of H3 in aggregates in NASP mutants seems to be entirely due to the reduction in total H3 levels rather than an increase in aggregated H3. If NASP's role is to prevent aggregation in the cytoplasm, and degradation has not yet begun in egg chambers, then why are aggregated H3 levels not increased in NASP mutants relative to wild-type egg chambers? If the same number of egg chambers were used, shouldn't the total amount of histone be the same in the absence of degradation?

In previously published work, we demonstrated that total H3 levels are unaffected when comparing WT and NASPmutant stage 14 egg chambers. This means that the amount of H3 deposited into the eggs does not change in the absence of NASP. To address the reviewer's comment, we will change the text to make the link to our previous work clear. As stated above, we will add a supplement figure showing H3 levels at different steps of the aggregate isolation assay.

The live imaging studies are well designed, executed, and quantified. They use an established genotype (H3.2-Dendra2) in wild-type and NASP maternal mutants to demonstrate that NASP is not directly involved in nuclear import of H3.2. Decreased import is likely due to reduced H3.2 levels in NASP mutants rather than reduced import rates per se. The same methodology was used to determine that loss of NASP did not affect H3.2 nuclear export. These findings eliminate H3.2 nuclear import/export regulation as possible roles for NASP, which had been previously proposed.

Thank you.

Live imaging also conclusively demonstrates that the levels of H3.2 in the nucleoplasm and in mitotic chromatin are significantly lower in NASP mutants than wild-type nuclei. Despite these lower histone levels, the nuclear cycle duration is only modestly lengthened. The live imagining of NASP-Dendra2 nuclear import conclusively demonstrate that NASP and H3.2 are unlikely to be imported into the nucleus as one complex.

Thank you.

Minor Comments:

Additional details on how the NASP-Dendra2 CRISPR allele was generated should be provided. In addition, additional details on how it was determined that this allele is functional should be provided (e.g. quantitative assays for fertility/embryo viability of NASP-Dendra2 females) We will make these additions to the text.

If statistical tests are used to determine significance, the type of test used should be reported in the figure legends throughout.

We will make the addition of the statistical tests to the figure legends.

The western blot shown in Figure 4A looks more like a 4-fold reduction in H3 levels in NASP mutants relative to wild-type embryos, rather than the quantified 2-fold reduction. Perhaps a more representative blot can be shown.

We have additional blots in the supplemental figure S3C. The quantification was performed after normalization to the total protein levels and we can highlight that in the figure legend.

Reviewer #2 (Significance (Required)):

As a fly chromatin biologist with colleagues that utilize mammalian experimental systems, I feel this manuscript will be of broad interest to the chromatin research community. Packaging of the genome into chromatin affects nearly every DNA-templated process, making the mechanisms by which histone proteins are expressed, chaperoned, and deposited into chromatin of high importance to the field. The study has multiple strengths, including high-quality quantitative imaging, use of a terrific experimental system (storage and deposition of soluble histones in early fly embryos). The study also answers outstanding questions in the field, specifically that NASP does not control nuclear import/export of histone H3. Instead, the authors propose that NASP functions to prevent protein aggregation. If this could be conclusively demonstrated, it would be valuable to the field. However, the protein aggregation studies need improvement. Technical demonstration that their differential centrifugation assay accurately detects aggregated proteins is needed. Further, NASP mutants do not exhibit increased H3 protein aggregation in the data presented. Instead, the increased fraction of aggregated H3 in NASP mutants seems to be due to a reduction in the overall levels of H3 protein, which is contrary to the model presented in this paper.

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

This manuscript by Das et al. entitled "NASP functions in the cytoplasm to prevent histone H3 aggregation during early embryogenesis", explores the role of the histone chaperone NASP in regulating histone H3 dynamics during early Drosophila embryogenesis. Using primarily live imaging approaches, the authors found that NASP is not directly involved in the import or export of H3. Moreover, the authors claimed that NASP prevents H3 aggregation rather than protects against degradation.

Major Comments:

Figure 1A-B: The plotted data appear to have substantial dispersion. Could the authors include individual data points or provide representative images to help the reader assess variability?

We chose to show unnormalized data in Figure 1 so readers could better compare the actual import values of H3 in the presence and absence of NASP. We felt it was a better representation of the true biological difference although raw data is more dispersive. We did also include normalized data in the supplement. Regardless, we will add representative stills to Figure 1 and include a H3-Dendra2 movie in the supplement to show the representative data.

Given that the authors conclude that the reduced nuclear import is due to lowered H3 levels in NASP-deficient embryos, would overexpression of H3 rescue this phenotype? This would directly test whether H3 levels, rather than import machinery per se, drive the effect.

We thank the reviewer for their valuable suggestion. We and others have tried to overexpress histones in the Drosophila early embryo without success. There must be an undefined feedback mechanism preventing histone overexpression in the germline. In fact, a recent paper has been deposited on bioRxiv (https://doi.org/10.1101/2024.12.23.630206) that suggest H4 protein could provide a feedback mechanism to prevent histone overexpression. While we would love to do this experiment, it is not technically feasible at this time.

Figure 2A-B: The authors present the Relative Intensity of H3-Dendra2, but this metric obscures absolute differences between Control and NASP knockout embryos. Please include Total Intensity plots to show the actual reduction in H3 levels.

We will add the total H3-Dendra2 intensity plots to the supplemental figure for the export curves.

Additionally, Western blot analysis of nucleoplasmic H3 from wild-type vs. NASP-deficient embryos would provide essential biochemical confirmation of H3 level reductions.

We will measure nuclear H3 levels by western from 0-2 hr embryos laid by WT and NASP mutant flies.

Figure 4: To support the conclusion that NASP prevents H3 aggregation, I recommend performing aggregation assays by adding compounds that induce unfolding (amino acid analogues that induce unfolding, like canavanine or Azetidine-2-carboxylic acid) or using aggregation-prone H3 mutants.

This is a very helpful suggestion! It is difficult to get chemicals into Drosophila eggs, but we will treat extracts directly with these chemicals. Additionally, we will use heat shocked eggs and extracts as an additional control.

Inclusion of CMA and proteasome inhibition experiments could also clarify whether degradation pathways are secondarily involved or compensatory in the absence of NASP.

The degradation pathway for H3 in the absence of NASP is unknown and a major focus of our future work is to define this pathway. Drosophila does not have a CMA pathway and therefore, we don't know how H3 aggregates are being sensed.

Minor Comments:

(1) The Introduction would benefit from mentioning the two NASP isoforms that exist in mammals (sNASP and tNASP), as this evolutionary context may inform interpretation of the Drosophila results.

We will make the edits in the text to include that Drosophila NASP is the sole homolog of sNASP and that tNASP ortholog is not found in Drosophila.

(2) Could the authors comment on the status of histone H4 in their experimental system? Given the observed cytoplasmic pool of H3, is it likely to exist as a monomer? If this H3 pool is monomeric, does that suggest an early failure in H3-H4 dimerization, and could this contribute to its aggregation propensity?

In our previous work we noted that NASP binds more preferentially to H3 and the levels of H3 we much more reduced upon NASP depletion than H4. We pointed out in this publication that our data was consistent with H3 stores being monomeric in the Drosophila embryo. We don't' have a H4-Dendra2 line to test. In the future, however, this is something we are very keen to look at.

Reviewer #3 (Significance (Required)):

This work addresses a timely and important question in the field of chromatin biology and developmental epigenetics. The focus on histone homeostasis during embryogenesis and the cytoplasmic role of NASP adds a novel perspective. The live imaging experiments are a clear strength, providing valuable spatiotemporal insights. However, I believe that the manuscript would benefit significantly from additional biochemical validation to support and clarify some of the mechanistic claims.

3. Description of the revisions that have already been incorporated in the transferred manuscript

• *

4. Description of analyses that authors prefer not to carry out

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

Author response:

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

Reviewer #1 (Public review):

(1) The methods section is overly brief. Even if techniques are cited, more experimental details should be included. For example, since the study focuses heavily on methodology, details such as the number of PCR cycles in RT-PCR or the rationale for choosing HA and PB2 as representative in vitro transcripts should be provided.

We thank the reviewer for this important suggestion. We have now expanded the Methods section to include the number of PCR cycles used in RT-PCR (line 407) and have explained the rationale for choosing HA and PB2 as representative transcripts (line 388).

(2) Information on library preparation and sequencing metrics should be included. For example, the total number of reads, any filtering steps, and quality score distributions/cutoff for the analyzed reads.

We agree and have added detailed information on library preparation, filtering criteria, quality score thresholds, and sequencing statistics for each sample (line 422, Figure S2).

(3) In the Results section (line 115, "Quantification of error rate caused by RT"), the mutation rate attributed to viral replication is calculated. However, in line 138, it is unclear whether the reported value reflects PB2, HA, or both, and whether the comparison is based on the error rate of the same viral RNA or the mean of multiple values (as shown in Figure 3A). Please clarify whether this number applies universally to all influenza RNAs or provide the observed range.

We appreciate this point. We have clarified in the Results (line 140) that the reported value corresponds to PB2.

(4) Since the T7 polymerase introduced errors are only applied to the in vitro transcription control, how were these accounted for when comparing mutation rates between transcribed RNA and cell-culture-derived virus?

We agree that errors introduced by T7 RNA polymerase are present only in the in vitro–transcribed RNA control. However, even when taking this into account, the error rate detected in the in vitro transcripts remained substantially lower than that observed in the viral RNA extracted from replicated virus (line 140, Fig.3a). Thus, the difference cannot be explained by T7-derived errors, and our conclusion regarding the elevated mutation rate in cell-culture–derived viral populations remains valid.

(5) Figure 2 shows that a UMI group size of 4 has an error rate of zero, but this group size is not mentioned in the text. Please clarify.

We have revised the Results (line 98) to describe the UMI group size of 4.

Reviewer #2 (Public review):

(1) The application of UMI-based error correction to viral population sequencing has been established in previous studies (e.g., HIV), and this manuscript does not introduce a substantial methodological or conceptual advance beyond its use in the context of influenza.

We appreciate the reviewer’s comment and agree that UMI-based error correction has been applied previously to viral population sequencing, including HIV. However, to our knowledge, relatively few studies have quantitatively evaluated both the performance of this method and the resulting within-quasi-species mutation distributions in detail. In our manuscript, we not only validate the accuracy of UMIbased error correction in the context of influenza virus sequencing, but also quantitatively characterize the features of intra-quasi-species distributions, which provides new insights into the mutational landscape and evolutionary dynamics specific to influenza. We therefore believe that our work goes beyond a simple application of an established method.

(2) The study lacks independent biological replicates or additional viral systems that would strengthen the generalizability of the conclusions.

We agree with the reviewer that the lack of independent biological replicates and additional viral systems limits the generalizability of our findings. In this study, we intentionally focused on single-particle–derived populations of influenza virus to establish a proof-of-principle for our sequencing and analytical framework. While this design provided a clear demonstration of the method’s ability to capture mutation distributions at the single-particle level, we acknowledge that additional biological replicates and testing across diverse viral systems would be necessary to confirm the broader applicability of our observations. Importantly, even within this limited framework, our analysis enabled us to draw conclusions at the level of individual viral populations and to suggest the possibility of comparing their mutation distributions with known evolvability. This highlights the potential of our approach to bridge observations from single particles with broader patterns of viral evolution. In future work, we plan to expand the number of populations analyzed and include additional viral systems, which will allow us to more rigorously assess reproducibility and to establish systematic links between mutation accumulation at the single-particle level and evolutionary dynamics across viruses.

(3) Potential sources of technical error are not explored or explicitly controlled. Key methodological details are missing, including the number of PCR cycles, the input number of molecules, and UMI family size distributions.

We thank the reviewer for this important suggestion. We have now expanded the Methods section to include the number of PCR cycles used in RT-PCR (line 407). In addition, we have added information on the estimated number of input molecules. Regarding the UMI family size distributions, we have added the data as Figure S2 and referred to it in the revised manuscript.

Finally, with respect to potential sources of technical error, we note that this point is already addressed in the manuscript by direct comparison with in vitro transcribed RNA controls, which encompass errors introduced throughout the entire experimental process. This comparison demonstrates that the error-correction strategy employed here effectively reduces the impact of PCR or sequencing artifacts.

(4) The assertion that variants at ≥0.1% frequency can be reliably detected is based on total read count rather than the number of unique input molecules. Without information on UMI diversity and family sizes, the detection limit cannot be reliably assessed.

We thank the reviewer for raising this important issue. We agree that our original description was misleading, as the reliable detection limit should not be defined solely by total read count. In the revised version, we have added information on UMI distribution and family sizes (Figure S2), and we now state the detection limit in terms of consensus reads. Specifically, we define that variants can be reliably detected when ≥10,000 consensus reads are obtained with a group size of ≥3 (line 173). 

(5)  Although genetic variation is described, the functional relevance of observed mutations in HA and NA is not addressed or discussed.

We appreciate the reviewer’s suggestion. In our study, we did not apply drug or immune selection pressure; therefore, we did not expect to detect mutations that are already known to cause major antigenic changes in HA or NA, and we think it is difficult to discuss such functional implications in this context. However, as noted in discussion, we did identify drug resistance–associated mutations. This observation suggests that the quasi-species pool may provide functional variation, including resistance, even in the absence of explicit selective pressure. We have clarified this point in the text to better address the reviewer’s concern (line 330).

(6) The experimental scale is small, with only four viral populations derived from single particles analyzed. This limited sample size restricts the ability to draw broader conclusions.

We thank the reviewer for pointing out the limitation of analyzing only four viral populations derived from single particles. We fully acknowledge that the small sample size restricts the generalizability of our conclusions. Nevertheless, we would like to emphasize that even within this limited dataset, our results consistently revealed a slight but reproducible deviation of the mutation distribution from the Poisson expectation, as well as a weak correlation with inter-strain conservation. These recurring patterns highlight the robustness of our observations despite the sample size.

In future work, we plan to expand the number of viral populations analyzed and to monitor mutation distributions during serial passage under defined selective pressures. We believe that such expanded analyses will enable us to more reliably assess how mutations accumulate and to develop predictive frameworks for viral evolution.

Reviewer #1 (Recommendations for the authors):

(1)  Please mention Figure 1 and S2 in the text.

Done. We now explicitly reference Figures 1 and S2 (renamed to S1 according to appearance order) in the appropriate sections (lines 74, 124).

(2)  In Figure 4A, please specify which graph corresponds to PB2 and which to PB2-like sequences.

Corrected. Figure 4A legend now specify PB2 vs. PB2-like sequences.

(3)  Consider reducing redundancy in lines 74, 149, 170, 214, and 215.

We thank the reviewer for this stylistic suggestion. We have revised the text to reduce redundancy in these lines.

Reviewer #2 (Recommendations for the authors):

(1)  The manuscript states that "with 10,000 sequencing reads per gene ...variants at ≥0.1% frequency can be reliably detected." However, this interpretation conflates raw read counts with independent input molecules.

We have revised this statement throughout the text to clarify that sensitivity depends on the number of unique UMIs rather than raw read counts (line 173). To support this, we calculated the probability of detecting a true variant present at a frequency of 0.1% within a population. When sequencing ≥10,000 unique molecules, such a variant would be observed at least twice with a probability of approximately 99.95%. In contrast, the error rate of in vitro–transcribed RNA, reflecting errors introduced during the experimental process, was estimated to be on the order of 10⁻⁶ (line 140, Fig. 3a). Under this condition, the probability that the same artificial error would arise independently at the same position in two out of 10,000 molecules is <0.5%. Therefore, variants present at ≥0.1% can be reliably distinguished from technical artifacts and are confidently detected under our sequencing conditions.

(2) To support the claimed sensitivity, please provide for each gene and population: (a) UMI family size distributions, (b) number of PCR cycles and input molecule counts, and (c) recalculation of the detection limit based on unique molecules.

If possible, I encourage experimental validation of sensitivity claims, such as spike-in controls at known variant frequencies, dilution series, or technical replicates to demonstrate reproducibility at the 0.1% detection level.

We have added (a) histograms of UMI family size distributions for each gene and population (Figure S2), (b) detailed method RT-PCR protocol and estimated input counts (line 407), and (c) recalculated detection limits (line 173).

We appreciate the reviewer’s suggestion and fully recognize the value of spike-in experiments. However, given the observed mutation rate of T7-derived RNA and the sufficient sequencing depth in our dataset, it is evident that variants above the 0.1% threshold can be robustly detected without additional spike-in controls.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Review report for 'Sterols regulate ciliary membrane dynamics and hedgehog signaling in health and disease', Lamazière et al.

Reviewer #1

In this manuscript, Lamazière et al. address an important understudied aspect of primary cilium biology, namely the sterol composition in the ciliary membrane. It is known that sterols especially play an important role in signal transduction between PTCH1 and SMO, two upstream components of the Hedgehog pathway, at the primary cilium. Moreover, several syndromes linked to cholesterol biosynthesis defects present clinical phenotypes indicative of altered Hh signal transduction. To understand the link between ciliary membrane sterol composition and Hh signal transduction in health and disease, the authors developed a method to isolate primary cilia from MDCK cells and coupled this to quantitative metabolomics. The results were validated using biophysical methods and cellular Hh signaling assays. While this is an interesting study, it is not clear from the presented data how general the findings are: can cilia be isolated from different mammalian cell types using this protocol? Is the sterol composition of MDCK cells expected to the be the same in fibroblasts or other cell types? Without this information, it is difficult to judge whether the conclusions reached in fibroblasts are indeed directly related to the sterol composition detected in MDCK cells. Below is a detailed breakdown of suggested textual changes and experimental validations to strengthen the conclusions of the manuscript.

We would like to thank the reviewer for their helpful comments

Major comments:

• It appears that the comparison has been made between ciliary membranes and the rest of the cell's membranes, which includes many other membranes besides the plasma membrane. This significantly weakens the conclusions on the sterol content specific to the cilium, as it may in fact be highly similar to the rest of the plasma membrane. It is for example known that lathosterol is biosynthesized in the ER, and therefore the non-presence in the cilium may reflect a high abundance in the ER but not necessarily in the plasma membrane.

The reviewer is correct that we compared the sterol composition of the primary ciliary membrane to the average of the remaining cellular membranes. We agree that this broader reference fraction contains multiple intracellular membranes, including ER- and Golgi-derived compartments, and therefore does not isolate the plasma membrane specifically. We would like to emphasize that our study did not aim to compare the cilium directly to the plasma membrane, nor did we claim that the comparison was in any way related to the plasma membrane. It is also worth noting that previous studies in other ciliated organisms have reported a higher cholesterol content in cilia compared to the plasma membrane, suggesting that the two membranes may not be compositionally identical despite their continuity. However, we concur that determining the sterol composition of the MDCK plasma membrane would provide valuable context and enable a comparison with the membrane continuous with the ciliary membrane. Hence, we are willing to try isolating plasma membrane in the same cellular contexts.

• While the protocol to isolate primary cilium from MDCK cells is a valuable addition to the methods available, it would be good to at least include a discussion on its general applicability. Have the authors tried to use this protocol on fibroblasts for example?

Thank you for the reviewer's positive comment on the value of the ciliary isolation protocol. Indeed, we have attempted to apply the same approach to other ciliated cell types, namely IMCD3 and MEF cells. In the case of IMCD3 cells, we were able to isolate primary cilia using the same general strategy; however, we are still refining the preparation, as the overall yield is lower than in MDCK cells and the amount of material obtained is currently insufficient for comprehensive biochemical analyses. With MEF (fibroblast) cells, the procedure proved even more challenging, as the yield of isolated cilia was extremely low. This difficulty is likely due to the shorter length of fibroblast cilia and to their positioning beneath the cell body, which probably makes them more resistant to detachment. Overall, these observations suggest that while the protocol can be adapted to other cell types, its efficiency depends on cellular architecture. We have added a discussion of these aspects in the revised manuscript to clarify the method's current scope and limitations (lines 492-502).

• Some of the conclusions in the introduction (lines 75-80) seem to be incorrectly phrased based on the data: in basal conditions, ciliary membranes are already enriched in cholesterol and desmosterol, and the treatment lowers this in all membranes.

We agree, this was modified in the revised manuscript (lines 75-80).

• There seems to be little effect of simvastatin on overall cholesterol levels. Can the authors comment on this result? How would the membrane fluidity be altered when mimicking simvastatin-induced composition? Since the effect on Hh signaling appears to be the biggest (Figure 5B) under simvastatin treatment, it would be interesting to compare this against that found for AY9944 treatment. Also, the authors conclude that the effects of simvastatin treatment on ciliary membrane sterol composition are the mildest, however, one could argue that they are the strongest as there is a complete lack of desmosterol.

We thank the reviewer for these insightful comments. Regarding the modest overall effect of simvastatin on cholesterol levels, we would like to note that MDCK cells are an immortalized epithelial cell line with high metabolic plasticity. Such cancer-like cell types are known to exhibit enhanced de novo lipogenesis, particularly under culture conditions with ample glucose availability. This compensatory lipid biosynthesis can partially counterbalance pharmacological inhibition of the cholesterol biosynthetic pathway. Because simvastatin acts upstream in the pathway (at HMG-CoA reductase), its inhibition primarily reduces early intermediates rather than fully depleting end-product cholesterol, explaining the relatively mild changes observed in total cholesterol content.

Concerning desmosterol, we agree with the reviewer that its complete loss under simvastatin treatment is a striking finding that deserves further discussion. Interestingly, our data show that simvastatin treatment produces the strongest inhibition of pathway activation (as measured by SMO activation), but the weakest effect on signal transduction downstream of constitutively active SMOM2. This dichotomy suggests that the absence of desmosterol may preferentially affect the activation step of Hedgehog signaling at the ciliary membrane, without equally impacting downstream propagation. We have expanded the Result section to highlight this potential role of desmosterol in the activation phase of Hedgehog signaling and to contrast it with the effects observed under AY9944 treatment (lines 463-469).

It is not clear to me why the authors have chosen to use SAG to activate the Hh pathway, as this is a downstream mode of activation and bypasses PTCH1 (and therefore a potentially sterol-mediated interaction between the two proteins). It would be very informative to compare the effect of sterol modulation on the ability of ShhN vs SAG to activate the pathway.

Our study aims to demonstrate that the sterol composition of the ciliary membrane plays an essential role in the proper functioning of the Hedgehog (Hh) signaling pathway, comparable in importance to that of oxysterols and free cholesterol. Because ShhN itself is covalently modified by cholesterol, and Smoothened (SMO) can be directly activated by both oxysterols and cholesterol, we reasoned that using a non-native SMO agonist such as SAG would allow us to specifically assess defects arising from alterations in membrane-bound sterols. In this way, pathway activation by SAG provides a more direct readout of the functional contribution of ciliary membrane sterols to SMO activity, independent of potential confounding effects related to ShhN processing, secretion, or PTCH1-mediated regulation.

• The conclusions about the effect of tamoxifen on SMO trafficking in MEFs should be validated in human patient cells before being able to conclude that there is a potential off-target effect (line 438). Also, if that is the case, the experiment of tamoxifen treatment of EBP KO cells should give an additional effect on SMO trafficking. Also, could the CDPX2 phenotypes in patients be the result of different cell types being affected than the fibroblast used in this study?

We agree that carrying the proposed experiment would be a good way to assess a potential off-target effect. However, such validation is beyond the scope of the present study, as this comment on off-target effect was aimed primarily to propose a mechanistic hypothesis to explain the differences observed in Hedgehog pathway activation between patient-derived fibroblasts and tamoxifen-treated MEFs. We leaned towards this hypothesis because drug treatments are known for their overall variable specificity, but we agree other hypotheses are possible, and among them the difference in cell type, as both are fibroblasts but from different origin. We rephrased this passage in the revised manuscript (lines 447-448 ).

Regarding the reviewer's third point, we fully agree that the CDPX2 phenotype in patients is unlikely to arise solely from fibroblast dysfunction. Nevertheless, fibroblasts are the only patient-derived cells currently available to us, and they provide a useful model for assessing ciliary signaling. It is reasonable to expect that similar defects could occur in other, more physiologically relevant cell types.

• For the experiments with the SMO-M2 mutant, it would be useful to show the extent of pathway activation by the mutant compared to SAG or ShhN treatment of non-transfected cells. Moreover, it will be necessary to exclude any direct effects of the compound treatment on the ability of this mutant to traffic to the primary cilium, which can easily be done using fluorescence microscopy as the mutant is tagged with mCherry.

The SmoM2 mutant is indeed a well-characterized constitutively active form of Smoothened that has been extensively studied by us and others. It is well established that this mutant correctly localizes to the primary cilium and robustly activates the Hedgehog pathway in MEFs (see Eguether et al., Dev. Cell, 2014 or Eguether et al, mol.biol.cell, 2018). In our study, we have already included supporting evidence for pathway activation in Supplementary Figure S1b, showing Gli1 expression levels in untreated MEFs transfected with SmoM2, which illustrates the extent of its activation compared to ligand-induced conditions.

In line with the reviewer's recommendation, we will additionally include microscopy data showing SmoM2 localization in MEFs treated with the different sterol modulators. These data should confirm that the observed effects are not due to altered ciliary trafficking of the mutant protein but instead reflect changes in downstream signaling or membrane composition.

Minor comments:

Line 74: 'in patients', should be rephrased to 'patient-derived cells'

This was modified in the revised manuscript

Figure 2A: What do the '+/-' indicate? They seem to be erroneously placed.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Figure 2B: no label present for which bar represents cilia/other membranes

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Figure 2C: this representation is slightly deceptive, since the difference between cells and cilia for lanosterol is not significantly different as shown in figure 2A.

This representation has been removed in the revised figures.

Figure 3A: it would be useful to also show where 8-DHC is in the biosynthetic pathway.

This has been modified in the revised figures.

Line 373: the title should be rephrased as it infers that DHCR7 was blocked in model membranes, which is not the case.

This has been modified in the revised manuscript.

Lines 377-384: this paragraph seems to be a mix of methods and some explanation, but should be rephrased for clarity.

We believe the technical information within this paragraph are useful for the understanding of the reader. We would rather leave as is unless recommended by other reviewers or editorial staff.

Line 403: 'which could explain the resulting defects in Hedgehog signaling': how and what defects? At this point in the study no defects in Hh signaling have been shown.

This has been modified in the revised manuscript.

Figure 4D: 'd' is missing

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Line 408: SAG treatment resulted in slightly shorter cilia: this is not the case for just SAG treated cilia, but only for the combination of SAG + AY9944. However, in that condition there appears to be a subpopulation of very short cilia, are those real?

This is correct, this is not the case for untreated cilia, but the short population is real, not only in AY9944 but also in Tamoxifen and Simvastatin. Again, the relevance and significance of minor cilia length change is unclear and we are not trying to draw any other conclusion from this than saying that the ciliary compartment is modified.

Figure 5b: it would be good to add that all conditions contained SAG.

This has been modified in the revised figures.

Figure 5D: Since it is shown in Fig 5C that there are no positive cilia -SAG, there is no point to have empty graphs in Fig 5D on the left side, nor can any statistics be done. Similarly for 5K.

We think this is still worth having in the figure. As the reviewer noted in one of his next comment, there are cases where Smoothened or Patched can be abnormally distributed (see also Eguether et al, mol biol cell, 2018). This shows that we checked all conditions for presence or absence of Smo and that there is no signal to be found. We would rather leave it as is unless asked otherwise by editorial staff.

Figure 5E: it is not clearly indicated what is visualized in the inserts, sometimes it's a box, sometimes a line and they seem randomly integrated into the images.

We apologize for the oversight - the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Figure 5H: is this the intensity in just SMO positive cilia? If yes, this should be indicated, and the line at '0' for WT-SAG should be removed. I am also surprised there is then ns found for WT vs SLO, since in WT there are no positive cilia, but in SLO there are a few, so it appears to be more of a black-white situation. Perhaps it would be useful to split the data from different experiments to see if it consistently the case that there is a low percentage of SMO positive cilia in SLO cells.

Yes, as in the rest of figure 5, the fluorescence intensity of Smo is only taken into account in SMO positive cells. This is now indicated in figure legend (lines 890, 898, 903 ). As for Smo positive, this is a good suggestion. We checked and for cilia in non-activated SLO patients, there are 8 positive cilia over a total of 240 counted cilia, mainly from one of the experiments. We could remove the data or leave as is given that the result is not significant.

Fig S1: panels are inverted compared to mentioning in the text.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Methods-pharmacological treatments: there appear to be large differences in concentrations chosen to treat MDCK versus MEF cells - can the authors comment on these choices and show that the enzymes are indeed inhibited at the indicated concentrations?

We thank the reviewer for this important comment. The concentrations of the pharmacological treatments were optimized separately for MDCK and MEF cells based on cell-type-specific tolerance. For each compound, we used the highest concentration that produced no detectable cytotoxicity or morphological changes. These conditions ensured that the treatments were effective (as seen by changes in sterol composition in MDCK cilia and Hh pathway phenotypes in treated MEFs) and compatible with cell viability and ciliation. Although we did not directly assay enzymatic inhibition in each case, the selected concentrations are consistent with those previously reported to inhibit the targeted enzymes in similar cellular contexts.

Compound

Typical Concentration Range in Mammalian Cell Culture

Typical Exposure Duration

Example Cell Types

Representative Peer-Reviewed References

AY9944 (DHCR7 inhibitor)

1-10 µM widely used; 1 µM for minimal on-target effects; 2.5-10 µM for robust sterol shifts

24-72 h; some sterol studies up to several days

HEK293, fibroblasts, neuronal cells, macrophages

Kim et al., J Biol Chem, 2001 - used 1 µM in dose-response experiments.; Haas et al., Hum Mol Genet, 2007 - 1 µM in cell-based assays.; Recent macrophage sterol study - 2.5-10 µM to induce 7-DHC accumulation.

Simvastatin (HMG-CoA reductase inhibitor)

0.1-10 µM common; 1-10 µM most widely used for robust pathway inhibition

24-72 h

Diverse mammalian lines, including liver, fibroblasts, epithelial cells

Bytautaite et al., Cells (2020) - discusses common in-vitro ranges (1-10 µM).; Mullen et al., 2011 - used 10 µM simvastatin, noting it is a standard in-vitro concentration.

Tamoxifen (modulator of sterol metabolism)

1-20 µM; 1-5 µM for mild/longer treatments; 10-20 µM in cancer/cilia signaling studies

24-72 h (longer treatments often at 1-5 µM)

MDCK, MEFs, MCF-7, diverse epithelial lines

Schlottmann et al., Cells (2022) - used 5-25 µM in sterol-related cell studies.; MCF-7 literature - 0.1-1 µM for estrogenic signaling, higher (5-10 µM) for metabolic/sterol pathway effects.; Additional cancer cell work indicating similar ranges.

This information has been clarified in the revised Methods section (lines 222-224).

(optional): it would be interesting to include a gamma-tubulin staining on the cilium prep to see if there is indeed a presence of the basal body as suggested by the proteomics data.

Thank you, we will try this.

There are many spelling mistakes and inconsistencies throughout the manuscript and its figures (mix of French and English for example) so careful proofreading would be warranted. Moreover, there are many mentionings of 'Hedgehog defects' or 'Hedgehog-linked', where in fact it is a defect in or link to the Hedgehog pathway, not the protein itself. This should be corrected.

We thank the reviewer for noting these issues. We apologize for the inconsistencies observed in the initial submission, as mentioned previously, some of the figures inadvertently included earlier versions, which may have contributed to the errors identified. All figures have now been carefully revised and updated in the resubmitted manuscript.

Regarding the text, we are surprised to hear about the spelling inconsistencies, as the manuscript was professionally proofread prior to submission (documentation can be provided upon request). Nevertheless, we have conducted an additional round of thorough proofreading to ensure consistency throughout the text and figures.

Finally, we have corrected all instances of "Hedgehog defects" or "Hedgehog-linked" to the more accurate phrasing "Hedgehog pathway defect" or "Hedgehog pathway-linked," as suggested by the reviewer throughout the manuscript.

Reviewer #1 (Significance (Required)):

The study of ciliary membrane composition is highly relevant to understand signal transduction in health and disease. As such, the topic of this manuscript is significant and timely. However, as indicated above, there are limitations to this study, most notably the comparison of ciliary membrane versus all cellular membranes (rather than the plasma membrane), which weakens the conclusions that can be drawn. Moreover, cell-type dependency should be more thoroughly addressed. There certainly is a methodological advance in the form of cilia isolation from MDCK cells, however, it is unclear how broadly applicable this is to other mammalian cell types.

We would like to thank the reviewer for their helpful comments and we appreciate the reviewer's recognition of the relevance and timeliness of studying ciliary membrane composition in the context of signaling regulation. We fully acknowledge that our comparison was made between the primary ciliary membrane and the total cellular membrane fraction, which encompasses multiple intracellular membranes. Our intent, however, was to obtain a global overview of how the ciliary membrane differs from the average membrane environment within the cell, thereby highlighting features that are unique to the cilium as a signaling organelle. This approach provides valuable baseline information that complements, rather than replaces, future targeted comparisons with the plasma membrane. As mentioned in this reply, we aim at carrying out these experiments before publication. Regarding cell-type dependency, we concur that ciliary lipid composition may vary between cell types, reflecting differences in their functional specialization. Our method was intentionally established in MDCK cells, which are epithelial and highly ciliated, to ensure sufficient yield and reproducibility. We have initiated trials with other mammalian cell types, including IMCD3 and MEF cells, and while yields remain limited, preliminary results indicate that the approach is adaptable with further optimization. Thus, our current work establishes a robust and reproducible proof of concept in a mammalian model, providing the first detailed sterol fingerprint of a mammalian primary cilium.

We believe this constitutes a significant methodological and conceptual advance, as it opens the way for systematic exploration of ciliary lipid composition across diverse mammalian systems and pathological contexts.

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

Overview Accumulating evidence suggests that sterols play critical roles in signal transduction within the primary cilium, perhaps most notably in the Hedgehog cascade. However, the precise sterol composition of the primary cilium, and how it may change under distinct biological conditions, remains unknown, in part because of the lack of reproducible, widely accepted procedures to purify primary cilia from mammalian cultured cells. In the present study, the authors have designed a method to isolate the cilium from the MDCK cells efficiently and then utilized this procedure in conjunction with mass spectrometry to systematically analyze the sterol composition of the ciliary membrane, which they then compare to the sterol composition of the cell body. By analyzing this sterol profiling. the authors claim that the cilium has a distinct sterol composition from the cell body, including higher levels of cholesterol and desmosterol but lower levels of 8-DHC and & Lathosterol. This manuscript further demonstrates that alteration of sterol composition within cilia modulates Hedgehog signaling. These results strengthen the link between dysregulated Hedgehog signaling and defects in cholesterol biosynthesis pathways, as observed in SLOS and CDPX2.

While the ability to isolate primary cilia from cultured MDCK cells represents an important technical achievement, the central claim of the manuscript - that cilia have a different sterol composition from the cell body - is not adequately supported by the data, and more rigorous comparisons between the ciliary membrane and key organellar membranes (such as plasma membrane) are required to make this claim. Moreover, although the authors have repeatedly mention that the ciliary sterol composition is "tightly regulated" there is no evidence provided to support such claim. At best, the data suggest that the cilium and cell body may differ in sterol composition (though even that remains uncertain), but no underlying regulatory mechanisms are demonstrated. In addition, much of the 2nd half of the paper represents a rehash of experiments with sterol biosynthesis inhibitors that have already been published in the literature, making the conceptual advance modest at best. Lastly, the link between CDPX2 and defective Hedgehog signaling is tenuous.

We would like to thank the reviewer for their helpful comments

Major comments

Figure 1. C) Although the isolation of cilium from the MDCK cells using dibucaine treatment seems to be very efficient, the quality control of their fractionation procedure to monitor the isolation is limited to a single western blot of the purified cilia vs. cell body samples, with no representative data shown from the sucrose gradient fractionation steps. Given that prior studies (including those from the Marshall lab cited in this manuscript) found that 1) sucrose gradient fractionation was essential to obtain relatively pure ciliary fractions, and 2) the ciliary fractions appear to spread over many sucrose concentrations in those prior studies , the authors should have included the comparison of the fractionation profile from the sucrose gradient while isolating the primary cilium. This additional information would have further clarified and supported the efficiency of their proposed method.

We thank the reviewer for their insightful comments regarding the quality control of our ciliary fractionation. We would like to clarify several important methodological aspects that distinguish our approach from those used in the studies cited (including those from the Marshall lab). In the cited work, the authors used a continuous sucrose gradient ranging from 30 % to 45 %, which allowed visualization of the distribution of ciliary proteins across the gradient. In contrast, we employed a discontinuous sucrose gradient (25 % / 50 %) optimized for higher recovery and reproducibility in our hands. In our preparation, the primary cilia consistently localize at the interface between the 25 % and 50 % layers. We systematically collect five 1 mL fractions from this interface and use fractions 1-3 for downstream analyses, as fractions 4-5 are typically already depleted of ciliary material. This targeted collection ensures good enrichment and low contamination, while avoiding unnecessary dilution of the limited ciliary sample. We also note that the prior studies the reviewer refers to were optimized for proteomic analyses, and therefore used actin as a marker of contamination from the cell body. In our case, the downstream application is lipidomic profiling, for which such protein-based contamination markers are not directly informative, since no reliable lipid marker exists to differentiate between organelle membranes. For this reason, we limited the protein-level validation to a semi-quantitative assessment of ciliary enrichment using ARL13B Western blotting, which robustly reports the presence and enrichment of ciliary membranes. Finally, to complement this targeted validation, we performed proteomic analysis followed by Gene Ontology (GO) Enrichment Analysis using the PANTHER database. This analysis evaluates the overrepresentation of proteins associated with ciliary structures and functions relative to the background frequency in the Canis lupus familiaris proteome. The resulting enrichment profile confirms that the isolated material is highly enriched in ciliary components and somewhat depleted of non-ciliary contaminants, thereby serving as an unbiased and global assessment of sample specificity and purity. We believe that, together, these methodological choices provide a rigorous and quantitative validation of our fractionation efficiency and support the robustness of the cilia isolation protocol used in this study.

1. D) The authors presented proteomic data for the peptides analyzed from the isolated cilia in the form of GO term analysis; however, they did not provide examples of different proteins enriched within their fractionation procedure, aside from Arl13b shown in the blot. Including a summary table with representative proteins identified in the isolated ciliary fraction, along with the relative abundance or percentage distribution of these proteins, would make the data more informative.

We thank the reviewer for this valuable suggestion. As mentioned in the manuscript, our proteomic dataset includes numerous hallmark components of the cilium, such as 18 IFT proteins, 4 BBS proteins, and several Hedgehog pathway components (including SuFu and Arl13b), as well as axonemal (Tubulin, Kinesin, Dynein) and centrosomal proteins (Centrin, CEPs, γ-Tubulin, and associated factors). This composition demonstrates that the isolated fraction is highly enriched in bona fide ciliary components while retaining a small proportion of basal body proteins, which is expected given their physical continuity. Importantly, our dataset shows a 70% overlap with the ciliary proteome published by Ishikawa et al. and a 41% overlap with the CysCilia consortium's list of potential ciliary proteins, which supports both the specificity and reliability of our isolation procedure. Regarding the suggestion to present relative protein abundances, we would like to clarify that defining "relative to what" is challenging in this context. The stoichiometry of ciliary proteins is largely unknown, and relative abundance normalized to total protein content can be misleading, as ciliary structural and signaling components differ greatly in copy number and membrane association. For this reason, we chose to highlight in the text proteins such as BBS and IFTs, which are known to be of low abundance within the cilium; their detection supports the depth and specificity of our proteomic coverage. In addition, we performed an unbiased Gene Ontology (GO) Enrichment Analysis using the PANTHER database, which provides a systematic and quantitative overview of the biological processes and cellular components overrepresented in our dataset relative to the canine proteome. This analysis with regard to purity wa already discussed in the submitted manuscript discussion. To further address the reviewer's comment, we will include as a supplemental table in the revised manuscript, a summary table listing representative ciliary proteins identified in our fraction, including those overlapping with the CysCilia (Gold ans potential lists), CiliaCarta and Ishikawa/Marshall proteomes. This addition should make the dataset more transparent and informative while preserving scientific rigor.

Figure 2.

The authors represented the comparison of sterol content within the cilia versus whole cell (as cell membranes). Since different organelles have a very diverse degree of cholesterol contents within them, for instance plasma membrane itself is around 50 mol% cholesterol levels while organelles like ER have barely any cholesterol. Thus, comparing these two samples and claiming a 2.5-fold increase in cholesterol levels is misleading. A more appropriate comparison would be between isolated primary cilia and isolated plasma membranes (procedures to isolate plasma membranes have been described previously, e.g., Naito et al., eLife 2019; Das et al, PNAS 2013. The absence of such controls makes it difficult to fully validate the reported magnitude of sterols enrichment in cilia relative to the cell surface.

As already discussed above for reviewer 1, we would like to emphasize that our study did not aim to compare the cilium directly to the plasma membrane, nor did we claim that the comparison was in any way related to the plasma membrane. Our intent, was to obtain a global overview of how the ciliary membrane differs from the average membrane environment within the cell, thereby highlighting features that are unique to the cilium as a signaling organelle. This approach provides valuable baseline information that complements, rather than replaces, future targeted comparisons with the plasma membrane. However, we concur that determining the sterol composition of the MDCK plasma membrane would provide valuable context and enable a comparison with the membrane continuous with the ciliary membrane. Hence, we are willing to try isolating plasma membrane in the same cellular contexts, and we thank the reviewer for the proposed literature.

Also, because dibucaine was used here to isolate MDCK cilia, a control experiment to exclude possible effects of the dibucaine treatment on sterol biosynthesis would be helpful.

Thank you for this comment, we will verify this point by quantifying by GC-MS the sterol content of whole MDCK cells with and without 15 minutes-dibucaine treatments.

Figure 3.

Tamoxifen is a potent drug for nuclear hormone receptor activity and thus can independently influence various cellular processes. As several experiments in the later sections of the manuscript rely on tamoxifen treatment of cells, it is important that the authors include appropriate controls for tamoxifen treatment, to confirm that the observed effects do not stem from effects on nuclear hormone receptor activity. This would ensure that the observed effects can be confidently attributed to the experimental manipulation rather than to the intrinsic effects of tamoxifen.

The reviewer is right, tamoxifen, like many drugs, has pleiotropic effects in different cell processes. Aware of this possible issue, we turned to a genetic model creating a CRISPR-CAS9 mediated knock down of EBP, the enzyme targeted by tamoxifen. We showed in figure 5 that the results between tamoxifen treated cells and CRIPSR EBP cells were in accordance with one another, showing that, for hedgehog signaling, the effect of tamoxifen recapitulates the effect of the enzyme KO.

Figure4. The authors present the results of spectroscopy studies to analyze generalized polarization (GP) of liposomes in vitro , but only processed data are shown, and the raw spectra are not provided. The authors need to present representative spectra to enable the readers to interact the raw data from the experiments.

This has been added to new supplemental figure 1 and corresponding figure legend (lines 898-904)

Figure5. B) The experiment shown Gli1 mRNA levels following treatment with inhibitors of cholesterol biosynthesis, but similar findings have already been reported previously (e.g., Cooper et al, Nature Genetics 2003; Blassberg et al, Hum Mol Genet 2016), and the present results do not provide a significant conceptual advance over those earlier studies.

We thank the reviewer for this comment and for highlighting the importance of earlier studies on Hedgehog (Hh) signaling and cholesterol metabolism. While we fully agree that confirming and extending established findings has intrinsic scientific value, we respectfully disagree with the assertion that our work does not provide conceptual novelty.

The seminal work by Cooper et al. (Nature Genetics, 2003) indeed laid the foundation for linking sterol metabolism to Hedgehog signaling, and we cite it as such. However, that study was conducted in chick embryos, a model that is relatively distant from mammalian systems and human pathophysiology. Moreover, their approach relied heavily on cyclodextrin-mediated cholesterol depletion, which is non-specific and extracts multiple sterols from membranes (discussed in this article lines 512-516). In contrast, our study employs pharmacological inhibitors targeting specific enzymes in the sterol biosynthetic pathway, thereby allowing us to modulate distinct steps and intermediates in a controlled and mechanistically informative manner. We also extend these analyses to patient-derived fibroblasts and CRISPR-engineered cells, providing direct human and genetic validation of the observed effects. Importantly, we complement these cellular studies with biochemical characterization of isolated ciliary membranes from MDCK cells, enabling a direct assessment of how specific sterol alterations affect ciliary composition and Hh pathway function - an angle not addressed in prior work.

Regarding Blassberg et al. (Hum. Mol. Genet., 2016), we agree that part of our findings recapitulates their observations on SMO-related signaling defects, which we view as an important confirmation of reproducibility. However, their study primarily sought to distinguish whether Hh pathway impairment in SLOS results from 7-DHC accumulation or cholesterol depletion, concluding that cholesterol deficiency was the main cause. Our results expand on this by demonstrating that perturbations extend beyond these two sterols, and that additional intermediates in the biosynthetic pathway also impact ciliary membrane composition and signaling competence. Furthermore, our experiments using the constitutively active SmoM2 mutant show that Hh signaling defects are not restricted to SMO activation per se, revealing a broader disruption of the signaling machinery within the cilium.

Finally, neither of the above studies examined CDPX2 patient-derived cells or the consequences of EBP enzyme deficiency on Hh signaling. Our finding that this pathway is altered in this genetic context represents, to our knowledge, a novel link between CDPX2 and Hedgehog pathway dysfunction.

Taken together, our work builds upon and extends previous findings by integrating cell-type-specific, biochemical, and patient-based analyses to provide a more comprehensive and mechanistically detailed view of how sterol composition of the ciliary membrane regulates Hedgehog signaling.

In addition, the authors analyze the effect of these inhibitors on SAG stimulation, but the experiment lacks the control for Gli mRNA levels in the absence of SAG treatment. Without this control, it is impossible to know where the baseline in the experiment is and how large the effects in question really are.

Below, we provide the data expressed using the ΔΔCt method (NT + SAG normalized to NT - SAG), which more clearly illustrates the magnitude of the effect in question. As similar qPCR-based Hedgehog pathway activation assays in MEFs have been published previously (see Eguether et al., Dev. Cell 2014; Eguether et al., Mol. Biol. Cell 2018), our goal here was not to re-establish the assay itself but to highlight the comparative effects across experimental conditions. In addition, one of the datasets was obtained using a new batch of SAG, which exhibited stronger pathway activation across all conditions (visible as higher overall expression levels). To ensure valid statistical comparisons across experiments and to focus on relative rather than absolute activation, we therefore chose to present the data as fold change values, which provides a more robust and statistically consistent measure for cross-condition analysis.

J-K) The data represented in these panels for SAG treatment as fraction of Smo and its fluorescence intensity for the same sample appears to be inconsistent between the two graphs. Under SAG treatment for EBP mutants shows higher Smo fluorescence intensity while Smo positive cilia seems to be less than the wild type control cells. If the number of Smo+ cilia (quantified by eye) differs between conditions, shouldn't the quantification of Smo intensity within cilia show a similar difference?

We thank the reviewer for this careful observation. The apparent discrepancy arises because the two panels quantify different parameters. In panel (j), we counted the percentage of cilia positive for SMO (i.e., cilia in which SMO was detected above background). In contrast, panel (k) reports the fluorescence intensity of SMO, but this measurement was performed only within the SMO-positive cilia identified in panel (j). This distinction has now been explicitly clarified in the figure legend, as also suggested by Reviewer 1.

Taken together, these two analyses indicate that although fewer cilia display detectable SMO accumulation in the EBP mutant cells, the amount of SMO present within those cilia that do recruit it is comparable to wild-type levels (as reflected by the non-significant difference in fluorescence intensity). This interpretation helps explain the partial functional preservation of Hedgehog signaling in this condition and contrasts with cases such as AY9944 treatment, where both the number of SMO-positive cilia and the SMO intensity are reduced.

1. I) The rationale for using SmoM2 in the analysis of cholesterol metabolism-related diseases such as SLOS and CDPX2 is unclear. The SmoM2 variant is primarily associated with cancer rather than cholesterol biosynthesis defects and its relevance either of these disorders is not immediately apparent.

We thank the reviewer for this pertinent observation. We fully agree that SmoM2 was originally identified as an oncogenic mutation and is not directly associated with cholesterol biosynthesis disorders. However, our rationale for using this mutant was mechanistic rather than pathological. SmoM2 is a constitutively active form of SMO that triggers pathway activation independently of upstream components such as PTCH1 or ligand-mediated regulation.

By using SmoM2, we aimed to determine whether the signaling defects observed under conditions that alter sterol metabolism (e.g., treatment with AY9944 or tamoxifen) occur upstream or downstream of SMO activation. The results demonstrate that, even when SMO is constitutively active, the Hedgehog pathway remains impaired under AY9944 treatment-and to a lesser extent with tamoxifen-indicating that these sterol perturbations disrupt the pathway beyond the level of SMO activation itself. In contrast, cells treated with simvastatin maintain normal pathway responsiveness, reinforcing the specificity of this effect.

This experiment is therefore central to our study, as it reveals that sterol imbalance can hinder Hedgehog signaling even in the presence of an active SMO, providing new insight into how membrane composition influences downstream signaling competence.

Minor corrections

1. Line 385 seems to be a bit confusing which mentions cilia were treated with AY9944 - do the authors mean that cells were been treated with the drugs before isolation of cilia, or were the purified cilia actually treated with the drugs?

Thank you, this has been modified in the revised manuscript

The authors should add proper label in Figure 2 panel b for the bars representing the cilia and cell membranes.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Panels in Figure S1 should be re-arranged according to the figure legend and figure reference in line 450.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Legend for the Figure S1b should be corrected as data sets in graph represents 7 points while technical replicates in legend shows 6 experimental values.

Thank you, this has been modified in the revised manuscript

The labels for drug in Figure 3 and 5 should be corrected from tamoxifene to tamoxifen and simvastatine to simvastatin.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Reviewer #2 (Significance (Required)):

In the present study, the authors have designed a method to isolate the cilium from the MDCK cells efficiently and then utilized this procedure in conjunction with mass spectrometry to systematically analyze the sterol composition of the ciliary membrane, which they then compare to the sterol composition of the cell body. By analyzing this sterol profiling. the authors claim that the cilium has a distinct sterol composition from the cell body, including higher levels of cholesterol and desmosterol but lower levels of 8-DHC and & Lathosterol. This manuscript further demonstrates that alteration of sterol composition within cilia modulates Hedgehog signaling. These results strengthen the link between dysregulated Hedgehog signaling and defects in cholesterol biosynthesis pathways, as observed in SLOS and CDPX2.

While the ability to isolate primary cilia from cultured MDCK cells represents an important technical achievement, the central claim of the manuscript - that cilia have a different sterol composition from the cell body - is not adequately supported by the data, and more rigorous comparisons between the ciliary membrane and key organellar membranes (such as plasma membrane) are required to make this claim. Moreover, although the authors have repeatedly mention that the ciliary sterol composition is "tightly regulated" there is no evidence provided to support such claim. At best, the data suggest that the cilium and cell body may differ in sterol composition (though even that remains uncertain), but no underlying regulatory mechanisms are demonstrated. In addition, much of the 2nd half of the paper represents a rehash of experiments with sterol biosynthesis inhibitors that have already been published in the literature, making the conceptual advance modest at best. Lastly, the link between CDPX2 and defective Hedgehog signaling is tenuous.

We thank the reviewer for this detailed summary and for acknowledging the technical advance represented by our method for isolating primary cilia from MDCK cells. However, we respectfully disagree with several aspects of the reviewer's assessment of our work.

As we elaborated in our responses to earlier comments, particularly regarding Figure 5, we disagree with the characterization of part of our study as a "rehash", a somewhat derogatory word, of previously published experiments. Our approach differs from earlier studies by relying on specific pharmacological modulation of defined enzymes in the sterol biosynthesis pathway, rather than using non-specific agents such as cyclodextrins, and by linking these manipulations to direct biochemical measurements of ciliary sterol composition. This strategy allows, for the first time, a targeted and physiologically relevant examination of how specific sterol perturbations affect Hedgehog signaling.

Regarding our statement that ciliary sterol composition is "tightly regulated," we acknowledge that we have not yet explored the underlying molecular mechanisms of this regulation. Nevertheless, the experimental evidence supporting this statement lies in the variation of ciliary sterol composition across multiple treatments that strongly perturb cellular sterols. Despite broad cellular changes, the ciliary sterol profile remains very resilient for some parameters, an observation that, in our view, strongly supports the idea of a selective or regulated process maintaining ciliary sterol identity. This conclusion does not depend on comparison with other membrane compartments.

We also respectfully disagree that the observed differences between cilia and the cell body (which doesn't equal to plasma membrane) are "uncertain." The consistent enrichment in cholesterol and desmosterol, combined with the relative depletion in 8-DHC and lathosterol, were detected across independent replicates using robust lipidomic profiling and are statistically supported. These findings are, to our knowledge, the first quantitative demonstration of a sterol fingerprint specific to a mammalian cilium.

Finally, while we agree that the mechanistic link between CDPX2 and defective Hedgehog signaling warrants further exploration, the data we present, combining pharmacological inhibition (tamoxifen), CRISPR-mediated EBP knockout, and SMOM2 activation assays, all consistently indicate a functional impairment of the Hedgehog pathway under EBP deficiency. This is further reinforced by clinical reports describing Hedgehog-related phenotypes in CDPX2 patients. We therefore believe that our work provides a solid experimental and conceptual basis for connecting EBP dysfunction to Hedgehog signaling defects.

In summary, our study introduces a validated and reproducible method for mammalian cilia isolation, provides the first detailed sterol composition profile of primary cilia, and establishes a functional link between ciliary sterol imbalance and Hedgehog pathway modulation. We believe these findings represent a meaningful conceptual advance and a valuable resource for the field

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

Lamaziere et al. describe an improved protocol for isolating primary cilia from MDCK cells for downstream lipidomics analysis. Using this protocol, they characterize sterol profile of MDCK cilia membrane under standard growth conditions and following pharmacological perturbations that are meant to mimic SLOS and CDPX2 disorders in humans. The authors then assess the impact of the same pharmacological manipulations on Shh pathway activity and validate their findings from these experiments using orthogonal genetic approaches. Major and minor concerns that require attention prior to publication are outlined below.

We would like to thank the reviewer for their comments

Major 1.Since the extent of contamination of the cilia preps with non-cilia membranes is unclear, and variability between replicates is not reported, it makes interpretation of changes in cilia membrane sterol composition in response to pharmacological manipulations somewhat difficult to interpret. Discussing reproducibility of cilia sterol composition between replicates (and including corresponding data) could alleviate these concerns to some extent.

We thank the reviewer for this comment. We would like to clarify that variability between replicates is indeed reported throughout the manuscript. In Figures 2 and 3, all data are presented as mean {plus minus} SEM, as indicated in the figure legends. Specifically, the data in Figure 2 are derived from six independent experiments, reflecting the central dataset used for comparative analyses, while the data in Figure 3 are based on three independent experiments.

We also note that the overall variability between replicates is low, further supporting the reproducibility of our ciliary sterol composition measurements. This consistency across independent biological replicates provides confidence that the differences observed between cilia and the cell body are robust and not due to stochastic contamination or technical variation.

2.An abundant non-ciliary membrane protein (rather than GAPDH) may be a more appropriate loading control in Fig. 1C.

This is a valuable comment and we will find a non-ciliary membrane protein to complement this experiment.

3.Fig. 2b - which bar corresponds to cells and which one to cilia? What do numbers inside bars represent? Please label accordingly.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

4.Fig. 3b-d, right panels - please define what numbers inside bars represent

Thank you, this was done in the revised manuscript. The numbers are reports of absolute quantification.

5.The font in Figs 2, 3, and 4 is very small and difficult to read. Please make the font and/or panels bigger to improve readability.

We did our best to enlarge font despite space limitations, but we are willing to work with editorial staff to improve readability as suggested.

6.It would help to have a diagram of the key steps in the cholesterol synthesis pathway for reference early in the paper rather than in figure 3.

We thank the reviewer for his comment, but we don't understand why this would be helpful as we only use sterol modulators involving the pathway's enzyme in fig3. We are open to discussion with editorial staff about moving it up to fig2. If they feel this is needed

7.The authors need to discuss why/how global inhibition of enzymes (e.g. via AY9944 treatment) in a cell could cause reduction in cholesterol levels only in the cilium and not in other cell membranes (see also point 1). Yet, tamoxifen treatment lowers cholesterol across the board.

We thank the reviewer for these insightful comments. Regarding the modest overall effect of simvastatin on cholesterol levels, we would like to note that MDCK cells are an immortalized epithelial cell line with high metabolic plasticity. Such cancer-like cell types are known to exhibit enhanced de novo lipogenesis, particularly under culture conditions with ample glucose availability. This compensatory lipid biosynthesis can partially counterbalance pharmacological inhibition of the cholesterol biosynthetic pathway. Because simvastatin acts upstream in the pathway (at HMG-CoA reductase), its inhibition primarily reduces early intermediates rather than fully depleting end-product cholesterol, explaining the relatively mild changes observed in total cholesterol content. . This has been added in a new paragraph in the revised manuscript (lines 371-378).

8.Fig. 5c, g, and j - statistical analyses are missing and need to be added in support of conclusions drawn in the text of the manuscript.

Thank you, this has been done in the revised manuscript

9.The decrease in the fraction of Smo+ cilia observed in EBP KO cells is mild (panel j, no statistics), and there is possibly a clone-specific effect here as well (statistical analysis is needed to determine if EBP139 is indeed different from WT and whether EBP139 and 141 are different from each other). Similarly, Smo fluorescence intensity after SAG treatment (panel k) is the same in WT and EBP KO cells, while there is a marked difference in intraciliary Smo intensity after tamoxifen treatment. The author's conclusion "...we were able to show that results with human cells aligned with our tamoxifen experiments" (line 436) should be modified to more accurately reflect the presented data. Ditto conclusions on lines 440-442, 530-531. In fact, it is the lack of Hh phenotypes in CDPX2 patients that is consistent with the EBP KO data presented in the paper.

We thank the reviewer for this detailed comment. We have now performed the requested statistical analyses and incorporated them into the revised manuscript.

The new analyses confirm that both EBP139 and EBP141 CRISPR KO clones show a statistically significant reduction in the fraction of Smo⁺ cilia compared to WT cells. They also reveal that the two clones differ significantly from each other, consistent with the expected clonal variability inherent to independently derived CRISPR lines.

Despite this variability, several lines of evidence support our conclusion that the EBP KO phenotypes align with the effects observed after tamoxifen treatment:

1- Directionally consistent reduction in Smo⁺ cilia:

Although the magnitude of the decrease differs between clones, both clones display a significant reduction compared to WT, paralleling the reduction observed in tamoxifen-treated cells. This directional consistency is the key point for comparing pharmacological and genetic perturbations.

2-Converging evidence from SmoM2 experiments:

Tamoxifen treatment also reduces pathway output in the context of SmoM2 overexpression. This supports the interpretation that both EBP inhibition (tamoxifen) and EBP loss (CRISPR KO) impair Hedgehog signaling at the level of ciliary function, albeit more mildly than AY9944/SLOS-like perturbations.

3-Interpretation of Smo intensity (panel k):

As clarified in the revised text, the fluorescence intensities in panel K correspond only to cilia that are Smo-positive. The absence of a difference in intensity therefore does not contradict the observed reduction in the number of Smo⁺ cilia. Rather, it explains why the phenotype is milder than that observed for SLOS/AY9944: when Smo is able to enter the cilium, its enrichment level is comparable to WT.

4- Clinical relevance for CDPX2:

While Hedgehog-related phenotypes in CDPX2 patients may be milder or under-reported, several documented features, such as polydactyly (10% of cases), as well as syndactyly and clubfoot, are classically associated with ciliary/Hedgehog signaling defects. This clinical pattern is consistent with the milder yet detectable defects we observe in EBP KO cells.

Minor •Line 310: 'intraflagellar' rather than 'intraciliary' transport particle B is a more conventional term

We agree that intraflagellar is more conventional than intraciliary, but in this case, this is how the GO term is labeled in the database. In our opinion, it should stay as is.

• Fig. 2c - typos in the color key, is grey meant to be "cells" and blue "cilia"? Individual panels are not referenced in the text

This panel has been removed thanks to comment from reviewer 1 and 3 finding it misleading.

• Lines 357-358: "Notably, AY9944 treatment led to a greater reduction in cholesterol content as well as a greater increase in 7-DHC and 8-DHC in cilia than in the other cell membranes" - the authors need to support this statement with appropriate statistical analysis

We respectfully believe there may be a misunderstanding in the reviewer's concern. In all cases, our comparisons are made between treated vs. untreated conditions within each compartment (cell bulk vs. ciliary membrane), and the statistical significance of these differences is already reported as determined by a Mann-Whitney test. In every case, the changes observed are greater in cilia than in the cell body. The statement in the manuscript simply summarizes this quantitative observation. However, if the reviewer feels that an additional statistical test directly comparing the magnitude of the two compartment-specific changes would strengthen the claim, we are willing to include this analysis. Alternatively, if preferred, we can remove the sentence entirely, as the comparison is already clearly visible in Figure 3b.

• Line 473 - unclear what is meant by "olfactory cilia are mainly sensory and not primary". Primary cilia are sensory.

We agree, primary cilia are sensory, but still different from cilia belonging to sensory epithelia like retina photoreceptors or olfactory cilia. Nevertheless, this statement was modified in revised manuscript

• Line 551: 'data not shown'. Please include the data that you would like to discuss or remove discussion of these data from the manuscript.

The data is not shown because there is nothing to show, as we discussed in that sentence, use of cholesterol probe resulted in the disappearance of primary cilia altogether. We are willing to work with editorial staff to find a better way of expressing this idea.

Reviewer #3 (Significance (Required)):

Overall, the manuscript expands our knowledge of cilia membrane composition and reports an interesting link between SLOS and Shh signaling defects, which could at least in part explain SLOS patients' symptoms. The findings reported in the manuscript could be of interest to a broad audience of cell biologists and geneticists.

We would like to thank the reviewer for his recognition of the importance of this work

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, participants completed two different tasks. A perceptual choice task in which they compared the sizes of pairs of items and a value-different task in which they identified the higher value option among pairs of items with the two tasks involving the same stimuli. Based on previous fMRI research, the authors sought to determine whether the superior frontal sulcus (SFS) is involved in both perceptual and value-based decisions or just one or the other. Initial fMRI analyses were devised to isolate brain regions that were activated for both types of choices and also regions that were unique to each. Transcranial magnetic stimulation was applied to the SFS in between fMRI sessions and it was found to lead to a significant decrease in accuracy and RT on the perceptual choice task but only a decrease in RT on the value-different task. Hierarchical drift-diffusion modelling of the data indicated that the TMS had led to a lowering of decision boundaries in the perceptual task and a lower of non-decision times on the value-based task. Additional analyses show that SFS covaries with model-derived estimates of cumulative evidence and that this relationship is weakened by TMS.

Strengths:

The paper has many strengths including the rigorous multi-pronged approach of causal manipulation, fMRI and computational modelling which offers a fresh perspective on the neural drivers of decision making. Some additional strengths include the careful paradigm design which ensured that the two types of tasks were matched for their perceptual content while orthogonalizing trial-to-trial variations in choice difficulty. The paper also lays out a number of specific hypotheses at the outset regarding the behavioural outcomes that are tied to decision model parameters and are well justified.

Weaknesses:

(1.1) Unless I have missed it, the SFS does not actually appear in the list of brain areas significantly activated by the perceptual and value tasks in Supplementary Tables 1 and 2. Its presence or absence from the list of significant activations is not mentioned by the authors when outlining these results in the main text. What are we to make of the fact that it is not showing significant activation in these initial analyses?

You are right that the left SFS does not appear in our initial task-level contrasts. Those first analyses were deliberately agnostic to evidence accumulation (i.e., average BOLD by task, irrespective of trial-by-trial evidence). Consistent with prior work, SFS emerges only when we model the parametric variation in accumulated perceptual evidence.

Accordingly, we ran a second-level GLM that included trial-wise accumulated evidence (aE) as a parametric modulator. In that analysis, the left SFS shows significant aE-related activity specifically during perceptual decisions, but not during value-based decisions (SVC in a 10-mm sphere around x = −24, y = 24, z = 36).

To avoid confusion, we now:

(i) explicitly separate and label the two analysis levels in the Results; (ii) state up front that SFS is not expected to appear in the task-average contrast; and (iii) add a short pointer that SFS appears once aE is included as a parametric modulator. We also edited Methods to spell out precisely how aE is constructed and entered into GLM2. This should make the logic of the two-stage analysis clearer and aligns the manuscript with the literature where SFS typically emerges only in parametric evidence models.

(1.2) The value difference task also requires identification of the stimuli, and therefore perceptual decision-making. In light of this, the initial fMRI analyses do not seem terribly informative for the present purposes as areas that are activated for both types of tasks could conceivably be specifically supporting perceptual decision-making only. I would have thought brain areas that are playing a particular role in evidence accumulation would be best identified based on whether their BOLD response scaled with evidence strength in each condition which would make it more likely that areas particular to each type of choice can be identified. The rationale for the authors' approach could be better justified.

We agree that both tasks require early sensory identification of the items, but the decision-relevant evidence differs by design (size difference vs. value difference), and our modelling is targeted at the evidence integration stage rather than initial identification.

To address your concern empirically, we: (i) added session-wise plots of mean RTs showing a general speed-up across the experiment (now in the Supplement); (ii) fit a hierarchical DDM to jointly explain accuracy and RT. The DDM dissociates decision time (evidence integration) from non-decision time (encoding/response execution).

After cTBS, perceptual decisions show a selective reduction of the decision boundary (lower accuracy, faster RTs; no drift-rate change), whereas value-based decisions show no change to boundary/drift but a decrease in non-decision time, consistent with faster sensorimotor processing or task familiarity. Thus, the TMS effect in SFS is specific to the criterion for perceptual evidence accumulation, while the RT speed-up in the value task reflects decision-irrelevant processes. We now state this explicitly in the Results and add the RT-by-run figure for transparency.

(1.2.1) The value difference task also requires identification of the stimuli, and therefore perceptual decision-making. In light of this, the initial fMRI analyses do not seem terribly informative for the present purposes as areas that are activated for both types of tasks could conceivably be specifically supporting perceptual decision-making only.

Thank you for prompting this clarification.

The key point is what changes with cTBS. If SFS supported generic identification, we would expect parallel cTBS effects on drift rate (or boundary) in both tasks. Instead, we find: (a) boundary decreases selectively in perceptual decisions (consistent with SFS setting the amount of perceptual evidence required), and (b) non-decision time decreases selectively in the value task (consistent with speed-ups in encoding/response stages). Moreover, trial-by-trial SFS BOLD predicts perceptual accuracy (controlling for evidence), and neural-DDM model comparison shows SFS activity modulates boundary, not drift, during perceptual choices.

Together, these converging behavioral, computational, and neural results argue that SFS specifically supports the criterion for perceptual evidence accumulation rather than generic visual identification.

(1.2.2) I would have thought brain areas that are playing a particular role in evidence accumulation would be best identified based on whether their BOLD response scaled with evidence strength in each condition which would make it more likely that areas particular to each type of choice can be identified. The rationale for the authors' approach could be better justified.

We now more explicitly justify the two-level fMRI approach. The task-average contrast addresses which networks are generally more engaged by each domain (e.g., posterior parietal for PDM; vmPFC/PCC for VDM), given identical stimuli and motor outputs. This complements, but does not substitute for, the parametric evidence analysis, which is where one expects accumulation-related regions such as SFS to emerge. We added text clarifying that the first analysis establishes domain-specific recruitment at the task level, whereas the second isolates evidence-dependent signals (aE) and reveals that left SFS tracks accumulated evidence only for perceptual choices. We also added explicit references to the literature using similar two-step logic and noted that SFS typically appears only in parametric evidence models.

(1.3) TMS led to reductions in RT in the value-difference as well as the perceptual choice task. DDM modelling indicated that in the case of the value task, the effect was attributable to reduced non-decision time which the authors attribute to task learning. The reasoning here is a little unclear.

(1.3.1) Comment: If task learning is the cause, then why are similar non-decision time effects not observed in the perceptual choice task?

Great point. The DDM addresses exactly this: RT comprises decision time (DT) plus non-decision time (nDT). With cTBS, PDM shows reduced DT (via a lower boundary) but stable nDT; VDM shows reduced nDT with no change to boundary/drift. Hence, the superficially similar RT speed-ups in both tasks are explained by different latent processes: decision-relevant in PDM (lower criterion → faster decisions, lower accuracy) and decision-irrelevant in VDM (faster encoding/response). We added explicit language and a supplemental figure showing RT across runs, and we clarified in the text that only the PDM speed-up reflects a change to evidence integration.

(1.3.2) Given that the value-task actually requires perceptual decision-making, is it not possible that SFS disruption impacted the speed with which the items could be identified, hence delaying the onset of the value-comparison choice?

We agree there is a brief perceptual encoding phase at the start of both tasks. If cTBS impaired visual identification per se, we would expect longer nDT in both tasks or a decrease in drift rate. Instead, nDT decreases in the value task and is unchanged in the perceptual task; drift is unchanged in both. Thus, cTBS over SFS does not slow identification; rather, it lowers the criterion for perceptual accumulation (PDM) and, separately, we observe faster non-decision components in VDM (likely familiarity or motor preparation). We added a clarifying sentence noting that item identification was easy and highly overlearned (static, large food pictures), and we cite that nDT is the appropriate locus for identification effects in the DDM framework; our data do not show the pattern expected of impaired identification.

(1.4) The sample size is relatively small. The authors state that 20 subjects is 'in the acceptable range' but it is not clear what is meant by this.

We have clarified what we mean and provided citations. The sample (n = 20) matches or exceeds many prior causal TMS/fMRI studies targeting perceptual decision circuitry (e.g., Philiastides et al., 2011; Rahnev et al., 2016; Jackson et al., 2021; van der Plas et al., 2021; Murd et al., 2021). Importantly, we (i) use within-subject, pre/post cTBS differences-in-differences with matched tasks; (ii) estimate hierarchical models that borrow strength across participants; and (iii) converge across behavior, latent parameters, regional BOLD, and connectivity. We now replace the vague phrase with a concrete statement and references, and we report precision (HDIs/SEs) for all main effects.

Reviewer #2 (Public Review):

Summary:

The authors set out to test whether a TMS-induced reduction in excitability of the left Superior Frontal Sulcus influenced evidence integration in perceptual and value-based decisions. They directly compared behaviour - including fits to a computational decision process model - and fMRI pre and post-TMS in one of each type of decision-making task. Their goal was to test domain-specific theories of the prefrontal cortex by examining whether the proposed role of the SFS in evidence integration was selective for perceptual but not value-based evidence.

Strengths:

The paper presents multiple credible sources of evidence for the role of the left SFS in perceptual decision-making, finding similar mechanisms to prior literature and a nuanced discussion of where they diverge from prior findings. The value-based and perceptual decision-making tasks were carefully matched in terms of stimulus display and motor response, making their comparison credible.

Weaknesses:

(2.1) More information on the task and details of the behavioural modelling would be helpful for interpreting the results.

Thank you for this request for clarity. In the revision we explicitly state, up front, how the two tasks differ and how the modelling maps onto those differences.

(1) Task separability and “evidence.” We now define task-relevant evidence as size difference (SD) for perceptual decisions (PDM) and value difference (VD) for value-based decisions (VDM). Stimuli and motor mappings are identical across tasks; only the evidence to be integrated changes.

(2) Behavioural separability that mirrors task design. As reported, mixed-effects regressions show PDM accuracy increases with SD (β=0.560, p<0.001) but not VD (β=0.023, p=0.178), and PDM RTs shorten with SD (β=−0.057, p<0.001) but not VD (β=0.002, p=0.281). Conversely, VDM accuracy increases with VD (β=0.249, p<0.001) but not SD (β=0.005, p=0.826), and VDM RTs shorten with VD (β=−0.016, p=0.011) but not SD (β=−0.003, p=0.419).

(3 How the HDDM reflects this. The hierarchical DDM fits the joint accuracy–RT distributions with task-specific evidence (SD or VD) as the predictor of drift. The model separates decision time from non-decision time (nDT), which is essential for interpreting the different RT patterns across tasks without assuming differences in the accumulation process when accuracy is unchanged.

These clarifications are integrated in the Methods (Experimental paradigm; HDDM) and in Results (“Behaviour: validity of task-relevant pre-requisites” and “Modelling: faster RTs during value-based decisions is related to non-decision-related sensorimotor processes”).

(2.2) The evidence for a choice and 'accuracy' of that choice in both tasks was determined by a rating task that was done in advance of the main testing blocks (twice for each stimulus). For the perceptual decisions, this involved asking participants to quantify a size metric for the stimuli, but the veracity of these ratings was not reported, nor was the consistency of the value-based ones. It is my understanding that the size ratings were used to define the amount of perceptual evidence in a trial, rather than the true size differences, and without seeing more data the reliability of this approach is unclear. More concerning was the effect of 'evidence level' on behaviour in the value-based task (Figure 3a). While the 'proportion correct' increases monotonically with the evidence level for the perceptual decisions, for the value-based task it increases from the lowest evidence level and then appears to plateau at just above 80%. This difference in behaviour between the two tasks brings into question the validity of the DDM which is used to fit the data, which assumes that the drift rate increases linearly in proportion to the level of evidence.

We thank the reviewer for raising these concerns, and we address each of them point by point:

2.2.1. Comment: It is my understanding that the size ratings were used to define the amount of perceptual evidence in a trial, rather than the true size differences, and without seeing more data the reliability of this approach is unclear.

That is correct—we used participants’ area/size ratings to construct perceptual evidence (SD).

To validate this choice, we compared those ratings against an objective image-based size measure (proportion of non-black pixels within the bounding box). As shown in Author response image 3, perceptual size ratings are highly correlated with objective size across participants (Pearson r values predominantly ≈0.8 or higher; all p<0.001). Importantly, value ratings do not correlate with objective size (Author response image 2), confirming that the two rating scales capture distinct constructs. These checks support using participants’ size ratings as the participant-specific ground truth for defining SD in the PDM trials.

Author response image 1.

Objective size and value ratings are unrelated. Scatterplots show, for each participant, the correlation between objective image size (x-axis; proportion of non-black pixels within the item box) and value-based ratings (y-axis; 0–100 scale). Each dot is one food item (ratings averaged over the two value-rating repetitions). Across participants, value ratings do not track objective size, confirming that value and size are distinct constructs.

Author response image 2.

Perceptual size ratings closely track objective size. Scatterplots show, for each participant, the correlation between objective image size (x-axis) and perceptual area/size ratings (y-axis; 0–100 scale). Each dot is one food item (ratings averaged over the two perceptual ratings). Perceptual ratings are strongly correlated with objective size for nearly all participants (see main text), validating the use of these ratings to construct size-difference evidence (SD).

(2.2.2) More concerning was the effect of 'evidence level' on behaviour in the value-based task (Figure 3a). While the 'proportion correct' increases monotonically with the evidence level for the perceptual decisions, for the value-based task it increases from the lowest evidence level and then appears to plateau at just above 80%. This difference in behaviour between the two tasks brings into question the validity of the DDM which is used to fit the data, which assumes that the drift rate increases linearly in proportion to the level of evidence.

We agree that accuracy appears to asymptote in VDM, but the DDM fits indicate that the drift rate still increases monotonically with evidence in both tasks. In Supplementary figure 11, drift (δ) rises across the four evidence levels for PDM and for VDM (panels showing all data and pre/post-TMS). The apparent plateau in proportion correct during VDM reflects higher choice variability at stronger preference differences, not a failure of the drift–evidence mapping. Crucially, the model captures both the accuracy patterns and the RT distributions (see posterior predictive checks in Supplementary figures 11-16), indicating that a monotonic evidence–drift relation is sufficient to account for the data in each task.

Author response image 3.

HDDM parameters by evidence level. Group-level posterior means (± posterior SD) for drift (δ), boundary (α), and non-decision time (τ) across the four evidence levels, shown (a) collapsed across TMS sessions, (b) for PDM (blue) pre- vs post-TMS (light vs dark), and (c) for VDM (orange) pre- vs post-TMS. Crucially, drift increases monotonically with evidence in both tasks, while TMS selectively lowers α in PDM and reduces τ in VDM (see Supplementary Tables for numerical estimates).

(2.3) The paper provides very little information on the model fits (no parameter estimates, goodness of fit values or simulated behavioural predictions). The paper finds that TMS reduced the decision bound for perceptual decisions but only affected non-decision time for value-based decisions. It would aid the interpretation of this finding if the relative reliability of the fits for the two tasks was presented.

We appreciate the suggestion and have made the quantitative fit information explicit:

(1) Parameter estimates. Group-level means/SDs for drift (δ), boundary (α), and nDT (τ) are reported for PDM and VDM overall, by evidence level, pre- vs post-TMS, and per subject (see Supplementary Tables 8-11).

(2) Goodness of fit and predictive adequacy. DIC values accompany each fit in the tables. Posterior predictive checks demonstrate close correspondence between simulated and observed accuracy and RT distributions overall, by evidence level, and across subjects (Supplementary Figures 11-16).

Together, these materials document that the HDDM provides reliable fits in both tasks and accurately recovers the qualitative and quantitative patterns that underlie our inferences (reduced α for PDM only; selective τ reduction in VDM).

(2.4) Behaviourally, the perceptual task produced decreased response times and accuracy post-TMS, consistent with a reduced bound and consistent with some prior literature. Based on the results of the computational modelling, the authors conclude that RT differences in the value-based task are due to task-related learning, while those in the perceptual task are 'decision relevant'. It is not fully clear why there would be such significantly greater task-related learning in the value-based task relative to the perceptual one. And if such learning is occurring, could it potentially also tend to increase the consistency of choices, thereby counteracting any possible TMS-induced reduction of consistency?

Thank you for pointing out the need for a clearer framing. We have removed the speculative label “task-related learning” and now describe the pattern strictly in terms of the HDDM decomposition and neural results already reported:

(1) VDM: Post-TMS RTs are faster while accuracy is unchanged. The HDDM attributes this to a selective reduction in non-decision time (τ), with no change in decision-relevant parameters (α, δ) for VDM (see Supplementary Figure 11 and Supplementary Tables). Consistent with this, left SFS BOLD is not reduced for VDM, and trialwise SFS activity does not predict VDM accuracy—both observations argue against a change in VDM decision formation within left SFS.

(2) PDM: Post-TMS accuracy decreases and RTs shorten, which the HDDM captures as a lower decision boundary (α) with no change in drift (δ). Here, left SFS BOLD scales with accumulated evidence and decreases post-TMS, and trialwise SFS activity predicts PDM accuracy, all consistent with a decision-relevant effect in PDM.

Regarding the possibility that faster VDM RTs should increase choice consistency: empirically, consistency did not change in VDM, and the HDDM finds no decision-parameter shifts there. Thus, there is no hidden counteracting increase in VDM accuracy that could mask a TMS effect—the absence of a VDM accuracy change is itself informative and aligns with the modelling and fMRI.

Reviewer #3 (Public Review):

Summary:

Garcia et al., investigated whether the human left superior frontal sulcus (SFS) is involved in integrating evidence for decisions across either perceptual and/or value-based decision-making. Specifically, they had 20 participants perform two decision-making tasks (with matched stimuli and motor responses) in an fMRI scanner both before and after they received continuous theta burst transcranial magnetic stimulation (TMS) of the left SFS. The stimulation thought to decrease neural activity in the targeted region, led to reduced accuracy on the perceptual decision task only. The pattern of results across both model-free and model-based (Drift diffusion model) behavioural and fMRI analyses suggests that the left SLS plays a critical role in perceptual decisions only, with no equivalent effects found for value-based decisions. The DDM-based analyses revealed that the role of the left SLS in perceptual evidence accumulation is likely to be one of decision boundary setting. Hence the authors conclude that the left SFS plays a domain-specific causal role in the accumulation of evidence for perceptual decisions. These results are likely to add importance to the literature regarding the neural correlates of decision-making.

Strengths:

The use of TMS strengthens the evidence for the left SFS playing a causal role in the evidence accumulation process. By combining TMS with fMRI and advanced computational modelling of behaviour, the authors go beyond previous correlational studies in the field and provide converging behavioural, computational, and neural evidence of the specific role that the left SFS may play.

Sophisticated and rigorous analysis approaches are used throughout.

Weaknesses:

(3.1) Though the stimuli and motor responses were equalised between the perception and value-based decision tasks, reaction times (according to Figure 1) and potential difficulty (Figure 2) were not matched. Hence, differences in task difficulty might represent an alternative explanation for the effects being specific to the perception task rather than domain-specificity per se.

We agree that RTs cannot be matched a priori, and we did not intend them to be. Instead, we equated the inputs to the decision process and verified that each task relied exclusively on its task-relevant evidence. As reported in Results—Behaviour: validity of task-relevant pre-requisites (Fig. 1b–c), accuracy and RTs vary monotonically with the appropriate evidence regressor (SD for PDM; VD for VDM), with no effect of the task-irrelevant regressor. This separability check addresses differences in baseline RTs by showing that, for both tasks, behaviour tracks evidence as designed.

To rule out a generic difficulty account of the TMS effect, we relied on the within-subject differences-in-differences (DID) framework described in Methods (Differences-in-differences). The key Task × TMS interaction compares the pre→post change in PDM with the pre→post change in VDM while controlling for trialwise evidence and RT covariates. Any time-on-task or unspecific difficulty drift shared by both tasks is subtracted out by this contrast. Using this specification, TMS selectively reduced accuracy for PDM but not VDM (Fig. 3a; Supplementary Fig. 2a,c; Supplementary Tables 5–7).

Finally, the hierarchical DDM (already in the paper) dissociates latent mechanisms. The post-TMS boundary reduction appears only in PDM, whereas VDM shows a change in non-decision time without a decision-relevant parameter change (Fig. 3c; Supplementary Figs. 4–5). If unmatched difficulty were the sole driver, we would expect parallel effects across tasks, which we do not observe.

(3.2) No within- or between-participants sham/control TMS condition was employed. This would have strengthened the inference that the apparent TMS effects on behavioural and neural measures can truly be attributed to the left SFS stimulation and not to non-specific peripheral stimulation and/or time-on-task effects.

We agree that a sham/control condition would further strengthen causal attribution and note this as a limitation. In mitigation, our design incorporates several safeguards already reported in the manuscript:

· Within-subject pre/post with alternating task blocks and DID modelling (Methods) to difference out non-specific time-on-task effects.

· Task specificity across levels of analysis: behaviour (PDM accuracy reduction only), computational (boundary reduction only in PDM; no drift change), BOLD (reduced left-SFS accumulated-evidence signal for PDM but not VDM; Fig. 4a–c), and functional coupling (SFS–occipital PPI increase during PDM only; Fig. 5).

· Matched stimuli and motor outputs across tasks, so any peripheral sensations or general arousal effects should have influenced both tasks similarly; they did not.

Together, these converging task-selective effects reduce the likelihood that the results reflect non-specific stimulation or time-on-task. We will add an explicit statement in the Limitations noting the absence of sham/control and outlining it as a priority for future work.

(3.3) No a priori power analysis is presented.

We appreciate this point. Our sample size (n = 20) matched prior causal TMS and combined TMS–fMRI studies using similar paradigms and analyses (e.g., Philiastides et al., 2011; Rahnev et al., 2016; Jackson et al., 2021; van der Plas et al., 2021; Murd et al., 2021), and was chosen a priori on that basis and the practical constraints of cTBS + fMRI. The within-subject DID approach and hierarchical modelling further improve efficiency by leveraging all trials.

To address the reviewer’s request for transparency, we will (i) state this rationale in Methods—Participants, and (ii) ensure that all primary effects are reported with 95% CIs or posterior probabilities (already provided for the HDDM as pmcmcp_{\mathrm{mcmc}}pmcmc). We also note that the design was sensitive enough to detect RT changes in both tasks and a selective accuracy change in PDM, arguing against a blanket lack of power as an explanation for null VDM accuracy effects. We will nevertheless flag the absence of a formal prospective power analysis in the Limitations.

Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

Some important elements of the methods are missing. How was the site for targeting the SFS with TMS identified? The methods described how M1 was located but not SFS.

Thank you for catching this omission. In the revised Methods we explicitly describe how the left SFS target was localized. Briefly, we used each participant’s T1-weighted anatomical scan and frameless neuronavigation to place a 10-mm sphere at the a priori MNI coordinates (x = −24, y = 24, z = 36) derived from prior work (Heekeren et al., 2004; Philiastides et al., 2011). This sphere was transformed to native space for each participant. The coil was positioned tangentially with the handle pointing posterior-lateral, and coil placement was continuously monitored with neuronavigation throughout stimulation. (All of these procedures mirror what we already report for M1 and are now stated for SFS as well.)

Where to revise the manuscript:

Methods → Stimulation protocol. After the first sentence naming cTBS, insert:<br /> “The left SFS target was localized on each participant’s T1-weighted anatomical image using frameless neuronavigation. A 10-mm radius sphere was centered at the a priori MNI coordinates x = −24, y = 24, z = 36 (Heekeren et al., 2004; Philiastides et al., 2011), then transformed to native space. The MR-compatible figure-of-eight coil was positioned tangentially over the target with the handle oriented posterior-laterally, and its position was tracked and maintained with neuronavigation during stimulation.”

It is not clear how participants were instructed that they should perform the value-difference task. Were they told that they should choose based on their original item value ratings or was it left up to them?

We agree the instruction should be explicit. Participants were told_: “In value-based blocks, choose the item you would prefer to eat at the end of the experiment.”_ They were informed that one VDM trial would be randomly selected for actual consumption, ensuring incentive-compatibility. We did not ask them to recall or follow their earlier ratings; those ratings were used only to construct evidence (value difference) and to define choice consistency offline.

Where to revise the manuscript:

Methods → Experimental paradigm.

Add a sentence to the VDM instruction paragraph:

“In value-based (LIKE) blocks, participants were instructed to choose the item they would prefer to consume at the end of the experiment; one VDM trial was randomly selected and implemented, making choices incentive-compatible. Prior ratings were used solely to construct value-difference evidence and to score choice consistency; participants were not asked to recall or match their earlier ratings.”

Line 86 Introduction, some previous studies were conducted on animals. Why it is problematic that the studies were conducted in animals is not stated. I assume the authors mean that we do not know if their findings will translate to the human brain? I think in fairness to those working with animals it might be worth an extra sentence to briefly expand on this point.

We appreciate this and will clarify that animal work is invaluable for circuit-level causality, but species differences and putative non-homologous areas (e.g., human SFS vs. rodent FOF) limit direct translation. Our point is not that animal studies are problematic, but that establishing causal roles in humans remains necessary.

Revision:

Introduction (paragraph discussing prior animal work). Replace the current sentence beginning “However, prior studies were largely correlational”

“Animal studies provide critical causal insights, yet direct translation to humans can be limited by species-specific anatomy and potential non-homologies (e.g., human SFS vs. frontal orienting fields in rodents). Therefore, establishing causal contributions in the human brain remains essential.”

Line 100-101: "or whether its involvement is peripheral and merely functionally supporting a larger system" - it is not clear what you mean by 'supporting a larger system'

We meant that observed SFS activity might reflect upstream/downstream support processes (e.g., attentional control or working-memory maintenance) rather than the computation of evidence accumulation itself. We have rephrased to avoid ambiguity.

Revision:

Introduction. Replace the phrase with:

“or whether its observed activity reflects upstream or downstream support processes (e.g., attention or working-memory maintenance) rather than the accumulation computation per se.”

The authors do have to make certain assumptions about the BOLD patterns that would be expected of an evidence accumulation region. These assumptions are reasonable and have been adopted in several previous neuroimaging studies. Nevertheless, it should be acknowledged that alternative possibilities exist and this is an inevitable limitation of using fMRI to study decision making. For example, if it turns out that participants collapse their boundaries as time elapses, then the assumption that trials with weaker evidence should have larger BOLD responses may not hold - the effect of more prolonged activity could be cancelled out by the lower boundaries. Again, I think this is just a limitation that could be acknowledged in the Discussion, my opinion is that this is the best effort yet to identify choice-relevant regions with fMRI and the authors deserve much credit for their rigorous approach.

Agreed. We already ground our BOLD regressors in the DDM literature, but acknowledge that alternative mechanisms (e.g., time-dependent boundaries) can alter expected BOLD–evidence relations. We now add a short limitation paragraph stating this explicitly.

Revision:

Discussion (limitations paragraph). Add:

“Our fMRI inferences rest on model-based assumptions linking accumulated evidence to BOLD amplitude. Alternative mechanisms—such as time-dependent (collapsing) boundaries—could attenuate the prediction that weaker-evidence trials yield longer accumulation and larger BOLD signals. While our behavioural and neural results converge under the DDM framework, we acknowledge this as a general limitation of model-based fMRI.”

Reviewer #2 (Recommendations For The Authors):

Minor points

I suggest the proportion of missed trials should be reported.

Thank you for the suggestion. In our preprocessing we excluded trials with no response within the task’s response window and any trials failing a priori validity checks. Because non-response trials contain neither a choice nor an RT, they are not entered into the DDM fits or the fMRI GLMs and, by design, carry no weight in the reported results. To keep the focus on the data that informed all analyses, we now (i) state the trial-inclusion criteria explicitly and (ii) report the number of analysed (valid) trials per task and run. This conveys the effective sample size contributing to each condition without altering the analysis set.

Revision:

Methods → (at the end of “Experimental paradigm”): “Analyses were conducted on valid trials only, defined as trials with a registered response within the task’s response window and passing pre-specified validity checks; trials without a response were excluded and not analysed.”

Results → “Behaviour: validity of task-relevant pre-requisites” (add one sentence at the end of the first paragraph): “All behavioural and fMRI analyses were performed on valid trials only (see Methods for inclusion criteria).”

Figure 4 c is very confusing. Is the legend or caption backwards?

Thanks for flagging. We corrected the Figure 4c caption to match the colouring and contrasts used in the panel (perceptual = blue/green overlays; value-based = orange/red; ‘post–pre’ contrasts explicitly labeled). No data or analyses were changed, just the wording to remove ambiguity.

Revision:

Figure 4 caption (panel c sentence). Replace with:

“(c) Post–pre contrasts for the trialwise accumulated-evidence regressor show reduced left-SFS BOLD during perceptual decisions (green overlay), with a significantly stronger reduction for perceptual vs value-based decisions (blue overlay). No reduction is observed for value-based decisions.”

Even if not statistically significant it may be of interest to add the results for Value-based decision making on SFS in Supplementary Table 3.

Done. We now include the SFS small-volume results for VDM (trialwise accumulated-evidence regressor) alongside the PDM values in the same table, with exact peak, cluster size, and statistics.

Revision:

Supplementary Table 3 (title):

“Regions encoding trialwise accumulated evidence (parametric modulation) during perceptual and value-based decisions, including SFS SVC results for both tasks.”

Model comparisons: please explain how model complexity is accounted for.

We clarify that model evidence was compared using the Deviance Information Criterion (DIC), which penalizes model fit by an effective number of parameters (pD). Lower DIC indicates better out-of-sample predictive performance after accounting for model complexity.

Revision:

Methods → Hierarchical Bayesian neural-DDM (last paragraph). Add:

“Model comparison used the Deviance Information Criterion (DIC = D̄ + pD), where pD is the effective number of parameters; thus DIC penalizes model complexity. Lower DIC denotes better predictive accuracy after accounting for complexity.”

Reviewer #3 (Recommendations For The Authors):

The following issues would benefit from clarification in the manuscript:

- It is stated that "Our sample size is well within acceptable range, similar to that of previous TMS studies." The sample size being similar to previous studies does not mean it is within an acceptable range. Whether the sample size is acceptable or not depends on the expected effect size. It is perfectly possible that the previous studies cited were all underpowered. What implications might the lack of an a priori power analysis have for the interpretation of the results?

We agree and have revised our wording. We did not conduct an a priori power analysis. Instead, we relied on a within-participant design that typically yields higher sensitivity in TMS–fMRI settings and on convergence across behavioural, computational, and neural measures. We now acknowledge that the absence of formal power calculations limits claims about small effects (particularly for null findings in VDM), and we frame those null results cautiously.

Revision:

Discussion (limitations). Add:

“The within-participant design enhances statistical sensitivity, yet the absence of an a priori power analysis constrains our ability to rule out small effects, particularly for null results in VDM.”

- I was confused when trying to match the results described in the 'Behaviour: validity of task-relevant pre-requisites' section on page 6 to what is presented in Figure 1. Specifically, Figure 1C is cited 4 times but I believe two of these should be citing Figure 1B?

Thank you—this was a citation mix-up. The two places that referenced “Fig. 1C” but described accuracy should in fact point to Fig. 1B. We corrected both citations.

Revision:

Results → Behaviour: validity… Change the two incorrect “Fig. 1C” references (when describing accuracy) to “Fig. 1B”.

- Also, where is the 'SD' coefficient of -0.254 (p-value = 0.123) coming from in line 211? I can't match this to the figure.

This was a typographical error in an earlier draft. The correct coefficients are those shown in the figure and reported elsewhere in the text (evidence-specific effects: for PDM RTs, SD β = −0.057, p < 0.001; for VDM RTs, VD β = −0.016, p = 0.011; non-relevant evidence terms are n.s.). We removed the erroneous value.

Revision:

Results → Behaviour: validity… (sentence with −0.254). Delete the incorrect value and retain the evidence-specific coefficients consistent with Fig. 1B–C.

- It is reported that reaction times were significantly faster for the perceptual relative to the value-based decision task. Was overall accuracy also significantly different between the two tasks? It appears from Figure 3 that it might be, But I couldn't find this reported in the text.

To avoid conflating task with evidence composition, we did not emphasize between-task accuracy averages. Our primary tests examine evidence-specific effects and TMS-induced changes within task. For completeness, we now report descriptive mean accuracies by task and point readers to the figure panels that display accuracy as a function of evidence (which is the meaningful comparison in our matched-evidence design). We refrain from additional hypothesis testing here to keep the analyses aligned with our preregistered focus.

Revision:

Results → Behaviour: validity… Add:

“For completeness, group-mean accuracies by task are provided descriptively in Fig. 3a; inferential tests in the manuscript focus on evidence-specific effects and TMS-induced changes within task.”

Author response:

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

Reviewer #1 (Public review):

Lack of Sensitivity Analyses for some Key Methodological Decisions: Certain methodological choices in this manuscript diverge from approaches used in previous works. In these cases, I recommend the following: (i) The authors could provide a clear and detailed justification for these deviations from established methods, and (ii) supplementary sensitivity analyses could be included to ensure the robustness of the findings, demonstrating that the results are not driven primarily by these methodological changes. Below, I outline the main areas where such evaluations are needed:

This detailed guidance is incredibly valuable, and we are grateful. Work of this kind is in its relative infancy, and there are so many design choices depending on the data available, questions being addressed, and so on. Help us navigate that has been extremely useful. In our revised manuscript we are very happy to add additional justification for design choices made, and wherever possible test the impact of those choices. It is certainly the case that different approaches have been used across the handful of papers published in this space, and, unlike in other areas of systems neuroscience, we have yet to reach the point where any of these approaches are established. We agree with the reviewer that wherever possible these design choices should be tested. 

Use of Communicability Matrices for Structural Connectivity Gradients: The authors chose to construct structural connectivity gradients using communicability matrices, arguing that diffusion map embedding "requires a smooth, fully connected matrix." However, by definition, the creation of the affinity matrix already involves smoothing and ensures full connectedness. I recommend that the authors include an analysis of what happens when the communicability matrix step is omitted. This sensitivity test is crucial, as it would help determine whether the main findings hold under a simpler construction of the affinity matrix. If the results significantly change, it could indicate that the observations are sensitive to this design choice, thereby raising concerns about the robustness of the conclusions. Additionally, if the concern is related to the large range of weights in the raw structural connectivity (SC) matrix, a more conventional approach is to apply a log-transformation to the SC weights (e.g., log(1+𝑆𝐶_𝑖𝑗)), which may yield a more reliable affinity matrix without the need for communicability measures.

The reason we used communicability is indeed partly because we wanted to guarantee a smooth fully connected matrix, but also because our end goal for this project was to explore structure-function coupling in these low-dimensional manifolds.  Structural communicability – like standard metrics of functional connectivity – includes both direct and indirect pathways, whereas streamline counts only capture direct communication. In essence we wanted to capture not only how information might be routed from one location to another, but also the more likely situation in which information propagates through the system. 

In the revised manuscript we have given a clearer justification for why we wanted to use communicability as our structural measure (Page 4, Line 179):

“To capture both direct and indirect paths of connectivity and communication, we generated weighted communicability matrices using SIFT2-weighted fibre bundle capacity (FBC). These communicability matrices reflect a graph theory measure of information transfer previously shown to maximally predict functional connectivity (Esfahlani et al., 2022; Seguin et al., 2022). This also foreshadowed our structure-function coupling analyses, whereby network communication models have been shown to increase coupling strength relative to streamline counts (Seguin et al., 2020)”.

We have also referred the reader to a new section of the Results that includes the structural gradients based on the streamline counts (Page 7, line 316):

“Finally, as a sensitivity analysis, to determine the effect of communicability on the gradients, we derived affinity matrices for both datasets using a simpler measure: the log of raw streamline counts. The first 3 components derived from streamline counts compared to communicability were highly consistent across both NKI  (r_s = 0.791, r_s = 0.866, r_s = 0.761) and the referred subset of CALM (r_s = 0.951, r_s = 0.809, r_s = 0.861), suggesting that in practice the organisational gradients are highly similar regardless of the SC metric used to construct the affinity matrices”. 

Methodological ambiguity/lack of clarity in the description of certain evaluation steps: Some aspects of the manuscript’s methodological description are ambiguous, making it challenging for future readers to fully reproduce the analyses based on the information provided. I believe the following sections would benefit from additional detail and clarification:

Computation of Manifold Eccentricity: The description of how eccentricity was computed (both in the results and methods sections) is unclear and may be problematic. The main ambiguity lies in how the group manifold origin was defined or computed. (1) In the results section, it appears that separate manifold origins were calculated for the NKI and CALM groups, suggesting a dataset-specific approach. (2) Conversely, the methods section implies that a single manifold origin was obtained by somehow combining the group origins across the three datasets, which seems contradictory. Moreover, including neurodivergent individuals in defining the central group manifold origin in conceptually problematic. Given that neurodivergent participants might exhibit atypical brain organization, as suggested by Figure 1, this inclusion could skew the definition of what should represent a typical or normative brain manifold. A more appropriate approach might involve constructing the group manifold origin using only the neurotypical participants from both the NKI and CALM datasets. Given the reported similarity between group-level manifolds of neurotypical individuals in CALM and NKI, it would be reasonable to expect that this combined origin should be close to the origin computed within neurotypical samples of either NKI or CALM. As a sanity check, I recommend reporting the distance of the combined neurotypical manifold origin to the centres of the neurotypical manifolds in each dataset. Moreover, if the manifold origin was constructed while utilizing all samples (including neurodivergent samples) I think this needs to be reconsidered. 

This is a great point, and we are very happy to clarify. Separate manifolds were calculated for the NKI and CALM participants, hence a dataset-specific approach. Indeed, in the long-run our goal was to explore individual differences in these manifolds, relative to the respective group-level origins, and their intersection across modalities, so manifold eccentricity was calculated at an individual level for subsequent analyses. At the group level, for each modality, we computed 3 manifold origins: one for NKI, one for the referred subset of CALM, and another for the neurotypical portion of CALM. Crucially, because the manifolds are always normal, in each case the manifold origin point is near-zero (extremely near-zero, to the 6^th or 7^th decimal place). In other words, we do indeed calculate the origin separately each time we calculate the gradients, but the origin is zero in every case. As a result, differences in the origin point cannot be the source of any differences we observe in manifold eccentricity between groups or individuals. We have updated the Methods section with the manifold origin points for each dataset and clarified our rationale (Page 16, Line 1296):

“Note that we used a dataset-specific approach when we computed manifold eccentricity for each of the three groups relative to their group-level origin: neurotypical CALM (SC origin = -7.698 x 10^-7, FC origin = 6.724 x 10^-7), neurodivergent CALM (SC origin = -6.422 x 10 , FC origin = 1.363 x 10 ), and NKI (SC origin = -7.434 x 10 , FC origin = 4.308 x 10^-6). Eccentricity is a relative measure and thus normalised relative to the origin. Because of this normalisation, each time gradients are constructed the manifold origin is necessarily near-zero, meaning that differences in manifold eccentricity of individual nodes, either between groups or individuals, are stem from the eccentricity of that node rather than a difference in origin point”. 

We clarified the computation of the respective manifold origins within the Results section, and referred the reader to the relevant Methods section (Page 9, line 446):

“For each modality (2 levels: SC and FC) and dataset (3 levels: neurotypical CALM, neurodivergent CALM, and NKI), we computed the group manifold origin as the mean of their respective first three gradients. Because of the normal nature of the manifolds this necessarily means that these origin points will be very near-zero, but we include the exact values in the ‘Manifold Eccentricity’ methodology sub-section”. 

Individual-Level Gradients vs. Group-Level Gradients: Unlike previous studies that examined alterations in principal gradients (e.g., Xia et al., 2022; Dong et al., 2021), this manuscript focuses on gradients derived directly from individual-level data. In contrast, earlier works have typically computed gradients based on grouped data, such as using a moving window of individuals based on age (Xia et al.) or evaluating two distinct age groups (Dong et al.). I believe it is essential to assess the sensitivity of the findings to this methodological choice. Such an evaluation could clarify whether the observed discrepancies with previous reports are due to true biological differences or simply a result of different analytical strategies.

This is a brilliant point. The central purpose of our project was to test how individual differences in these gradients, and their intersection across modalities, related to differences in phenotype (e.g. cognitive difficulties). These necessitated calculating gradients at the level of individuals and building a pipeline to do so, given that we could find no other examples. Nonetheless, despite this different goal and thus approach, we had expected to replicate a couple of other key findings, most prominently the ‘swapping’ of gradients shown by Dong et al. (2021). We were also surprised that we did not find this changing in order. The reviewer is right and there could be several design features that produce the difference, and in the revised manuscript we test several of them. We have added the following text to the manuscript as a sensitivity analysis for the Results sub-section titled “Stability of individual-level gradients across developmental time” (Page 7, Line 344 onwards):

“One possibility is that our observation of gradient stability – rather than a swapping of the order for the first two gradients (Dong et al., 2021) – is because we calculated them at an individual level. To test this, we created subgroups and contrasted the first two group-level structural and functional gradients derived from children (younger than 12 years old) versus those from adolescents (12 years old and above), using the same age groupings as prior work (Dong et al., 2021). If our use of individually calculated gradients produces the stability, then we should observe the swapping of gradients in this sensitivity analysis. Using baseline scans from NKI, the primary structural gradient in childhood (N = 99) as shown in Figure 1f, this was highly correlated (r_s = 0.995) with those derived from adolescents (N = 123). Likewise, the secondary structural gradient in childhood was highly consistent in adolescence (r_s = 0.988). In terms of functional connectivity, the principal gradient in childhood (N = 88) was highly consistent in adolescence (r_s = 0.990, N = 125). The secondary gradient in childhood was again highly similar in adolescence (r_s = 0.984). The same result occurred in the CALM dataset: In the baseline referred subset of CALM, the primary and secondary communicability gradients derived from children (N = 258) and adolescents (N = 53) were near-identical (r_s = 0.991 and r_s = 0.967, respectively). Alignment for the primary and secondary functional gradients derived from children (N = 130) and adolescents (N = 43) were also near-identical (r_s = 0.972 and r_s = 0.983, respectively). These consistencies across development suggest that gradients of communicability and functional connectivity established in childhood are the same as those in adolescence, irrespective of group-level or individual-level analysis. Put simply, our failure to replicate the swapping of gradient order in Dong et al. (2021) is not the result of calculating gradients at the level of individual participants.”

Procrustes Transformation: It is unclear why the authors opted to include a Procrustes transformation in this analysis, especially given that previous related studies (e.g., Dong et al.) did not apply this step. I believe it is crucial to evaluate whether this methodological choice influences the results, particularly in the context of developmental changes in organizational gradients. Specifically, the Procrustes transformation may maximize alignment to the group-level gradients, potentially masking individual-level differences. This could result in a reordering of the gradients (e.g., swapping the first and second gradients), which might obscure true developmental alterations. It would be informative to include an analysis showing the impact of performing vs. omitting the Procrustes transformation, as this could help clarify whether the observed effects are robust or an artifact of the alignment procedure. (Please also refer to my comment on adding a subplot to Figure 1). Additionally, clarifying how exactly the transformation was applied to align gradients across hemispheres, individuals, and/or datasets would help resolve ambiguity. 

The current study investigated individual differences in connectome organisation, rather than group-level trends (Dong et al., 2021). This necessitates aligning individual gradients to the corresponding group-level template using a Procrustes rotation. Without a rotation, there is no way of knowing if you are comparing  ‘like with like’: the manifold eccentricity of a given node may appear to change across individuals simply due to subtle differences in the arbitrary orientation of the underlying manifolds. We also note that prior work examining individual differences in principal alignment have used Procrustes (Xia et al., 2022), who demonstrated emergence of the principal gradient across development, albeit with much smaller effects than Dong and colleagues (2021). Nonetheless, we agree, the Procrustes rotation could be another source of the differences we observed with the previous paper (Dong et al. 2021). We explored the impact of the Procrustes rotation on individual gradients as our next sensitivity analysis. We recalculated everyone’s gradients without Procrustes rotation. We then tested the alignment of each participant with the group-level gradients using Spearman’s correlations, followed by a series of generalised linear models to predict principal gradient alignment using head motion, age, and sex. The expected swapping of the first and second functional gradient (Dong et al., 2021) would be represented by a decrease in the spatial similarity of each child’s principal functional gradient to the principal childhood group-level gradient, at the onset of adolescence (~age 12). However, there is no age effect on this unrotated alignment, suggesting that the lack of gradient swapping in our data does not appear to be the result of the Procrustes rotation. When you use unrotated individual gradients the alignment is remarkably consistent across childhood and adolescence. Alignment is, however, related to head motion, which is often related to age. To emphasise the importance of motion, particularly in relation to development, we conducted a mediation analysis between the relationship between age and principal alignment (without correcting for motion), with motion as a mediator, within the NKI dataset. Before accounting for motion, the relationship between age and principal alignment is significant, but this can be entirely accounted for by motion. In our revised manuscript we have included this additional analysis in the Results sub-section titled “Stability of individual-level gradients across developmental time”, following on from the above point about the effect of group-level versus individual-level analysis (Page 8, Line 400):

“A second possible discrepancy between our results and that of prior work examining developmental change in group-level functional gradients (Dong et al., 2021) was the use of Procrustes alignment. Such alignment of individual-level gradients to group-level templates is a necessary step to ensure valid comparisons between corresponding gradients across individuals, and has been implemented in sliding-window developmental work tracking functional gradient development (Xia et al., 2022). Nonetheless, we tested whether our observation of stable principal functional and communicability gradients may be an artefact of the Procrustes rotation. We did this by modelling how individual-level alignment without Procrustes rotation to the group-level templates varies with age, head motion, and sex, as a series of generalised linear models. We included head motion as the magnitude of the Procrustes rotation has been shown to be positively correlated with mean framewise displacement (Sasse et al., 2024), and prior group-level work (Dong et al., 2021) included an absolute motion threshold rather than continuous motion estimates. Using the baseline referred CALM sample, there was no significant relationship between alignment and age (β = -0.044, 95% CI = [-0.154, 0.066], p = 0.432) after accounting for head motion and sex. Interestingly, however head motion was significantly associated with alignment ( β = -0.318, 95% CI = [-0.428, -.207], p = 1.731 x 10^-8), such that greater head motion was linked to weaker alignment. Note that older children tended to have exhibit less motion for their structural scans (r_s = 0.335, p < 0.001). We observed similar trends in functional alignment, whereby tighter alignment was significantly predicted by lower head motion (β = -0.370, 95% CI = [-0.509, -0.231], p = 1.857 x 10^-7), but not by age (β= 0.049, 95% CI = [-0.090, 0.187], p = 0.490). Note that age and head motion for functional scans were not significantly related (r_s = -0.112, p = 0.137). When repeated for the baseline scans of NKI, alignment with the principal structural gradient was not significantly predicted by either scan age (β = 0.019, 95% CI = [-0.124, 0.163], p = 0.792) or head motion (β = -0.133, 95% CI = [-0.175, 0.009], p = 0.067) together in a single model, where age and motion were negatively correlated (r_s = -0.355, p < 0.001). Alignment with the principal functional gradient was significantly predicted by head motion (β = -0.183, 95% CI = [-0.329, -0.036], p = 0.014) but not by age (β= 0.066, 95% CI = [-0.081, 0.213], p = 0.377), where age and motion were also negatively correlated (r_s = -0.412, p < 0.001). Across modalities and datasets, alignment with the principal functional gradient in NKI was the only example in which there was a significant correlation between alignment and age (r_s = 0.164, p = 0.017) before accounting for head motion and sex. This suggests that apparent developmental effects on alignment are minimal, and where they do exist they are removed after accounting for head motion. Put together this suggests that the lack of order swapping for the first two gradients is not the result of the Procrustes rotation – even without the rotation there is no evidence for swapping”.

“To emphasise the importance of head motion in the appearance of developmental change in alignment, we examined whether accounting for head motion removes any apparent developmental change within NKI. Specifically, we tested whether head motion mediates the relationship between age and alignment (Figure 1X), controlling for sex, given that higher motion is associated with younger children (β= -0.429, 95% CI = [0.552, -0.305], p = 7.957 x 10^-11), and stronger alignment is associated with reduced motion (β = -0.211, 95% CI = [-0.344, -0.078], p = 2.017 x 10^-3). Motion mediated the relationship between age and alignment (β = 0.078, 95% CI = [0.006, 0.146], p = 1.200 x 10^-2), accounting for 38.5% variance in the age-alignment relationship, such that the link between age and alignment became non-significant after accounting for motion (β = 0.066, 95% CI = [-0.081, 0.214], p = 0.378). This firstly confirms our GLM analyses, where we control for motion and find no age associations. Moreover, this suggests that caution is required when associations between age and gradients are observed. In our analyses, because we calculate individual gradients, we can correct for individual differences in head motion in all our analyses. However, other than using an absolute motion threshold and motion-matched child and adolescent groups, individual differences in motion were not accounted for by prior work which demonstrated a flipping of the principal functional gradients with age (Dong et al., 2021)”. 

We further clarify the use of Procrustes rotation as a separate sub-section within the Methods (Page 25, Line 1273):

“Procrustes Rotation

For group-level analysis, for each hemisphere we constructed an affinity matrix using a normalized angle kernel and applied diffusion-map embedding. The left hemisphere was then aligned to the right using a Procrustes rotation. For individual-level analysis, eigenvectors for the left hemisphere were aligned with the corresponding group-level rotated eigenvectors. No alignment was applied across datasets. The only exception to this was for structural gradients derived from the referred CALM cohort. Specifically, we aligned the principal gradient of the left hemisphere to the secondary gradient of the right hemisphere: this was due to the first and second gradients explaining a very similar amount of variance, and hence their order was switched”. 

SC-FC Coupling Metric: The approach used to quantify nodal SC-FC coupling in this study appears to deviate from previously established methods in the field. The manuscript describes coupling as the "Spearman-rank correlation between Euclidean distances between each node and all others within structural and functional manifolds," but this description is unclear and lacks sufficient detail. Furthermore, this differs from what is typically referred to as SC-FC coupling in the literature. For instance, the cited study by Park et al. (2022) utilizes a multiple linear regression framework, where communicability, Euclidean distance, and shortest path length are independent variables predicting functional connectivity (FC), with the adjusted R-squared score serving as the coupling index for each node. On the other hand, the Baum et al. (2020) study, also cited, uses Spearman correlation, but between raw structural connectivity (SC) and FC values. If the authors opt to introduce a novel coupling metric, it is essential to demonstrate its similarity to these previous indices. I recommend providing an analysis (supplementary) showing the correlation between their chosen metric and those used in previous studies (e.g., the adjusted R-squared scores from Park et al. or the SC-FC correlation from Baum et al.). Furthermore, if the metrics are not similar and results are sensitive to this alternative metric, it raises concerns about the robustness of the findings. A sensitivity analysis would therefore be helpful (in case the novel coupling metric is not like previous ones) to determine whether the reported effects hold true across different coupling indices.

This is a great point, and we are happy to take the reviewer’s recommendation. There are multiple different ways of calculating structure-function coupling. For our set of questions, it was important that our metric incorporated information about the structural and functional manifolds, rather than being a separate approach that is unrelated to these low-dimensional embeddings. Put simply, we wanted our coupling measure to be about the manifolds and gradients outlined in the early sections of the results. We note that the multiple linear regression framework was developed by Vázquez-Rodríguez and colleagues (2019), whilst the structure-function coupling computed in manifold space by Park and colleagues (2022) was operationalised as a linear correlation between z-transformed functional connectomes and structural differentiation eigenvectors. To clarify how this coupling was calculated, and to justify why we developed a new coupling method based on manifolds rather than borrow an existing approach from the literature, we have revised the manuscript to make this far clearer for readers (Page 13, line 604):

“To examine the relationship between each node’s relative position in structural and functional manifold space, we turned our attention to structure-function coupling. Whilst prior work typically computed coupling using raw streamline counts and functional connectivity matrices, either as a correlation (Baum et al., 2020) or through a multiple linear regression framework (Vázquez-Rodríguez et al., 2019), we opted to directly incorporate low-dimensional embeddings within our coupling framework. Specifically, as opposed to correlating row-wise raw functional connectivity with structural connectivity eigenvectors (Park et al., 2022), our metric directly incorporates the relative position of each node in low-dimensional structural and functional manifold spaces. Each node was situated in a low-dimensional 3D space, the axes of which were each participant’s gradients, specific to each modality. For each participant and each node, we computed the Euclidean distance with all other nodes within structural and functional manifolds separately, producing a vector of size 200 x 1 per modality. The nodal coupling coefficient was the Spearman correlation between each node’s Euclidean distance to all other nodes in structural manifold space, and that in functional manifold space. Put simply, a strong nodal coupling coefficient suggests that that node occupies a similar location in structural space, relative to all other nodes, as it does in functional space”. 

We also agree with the reviewer’s recommendation to compare this to some of the more standard ways of calculating coupling. We compare our metric with 3 others (Baum et al., 2020; Park et al., 2022; VázquezRodríguez et al., 2019), and find that all metrics capture the core developmental sensorimotor-to-association axis (Sydnor et al., 2021). Interestingly, manifold-based coupling measures captured this axis more strongly than non-manifold measures. We have updated the Results accordingly (Page 14, Line 638):

“To evaluate our novel coupling metric, we compared its cortical spatial distribution to three others (Baum et al., 2020; Park et al., 2022; Vázquez-Rodríguez et al., 2019), using the group-level thresholded structural and functional connectomes from the referred CALM cohort. As shown in Figure 4c, our novel metric was moderately positively correlated to that of a multi-linear regression framework (r_s = 0.494, p_spin = 0.004; Vázquez-Rodríguez et al., 2019) and nodal correlations of streamline counts and functional connectivity (r_s = 0.470, p_spin = 0.005; Baum et al., 2020). As expected, our novel metric was strongly positively correlated to the manifold-derived coupling measure (r_s = 0.661, p_spin < 0.001; Park et al., 2022), more so than the first (Z(198) = 3.669, p < 0.001) and second measure (Z(198) = 4.012, p < 0.001). Structure-function coupling is thought to be patterned along a sensorimotor-association axis (Sydnor et al., 2021): all four metrics displayed weak-tomoderate alignment (Figure 4c). Interestingly, the manifold-based measures appeared most strongly aligned with the sensorimotor-association axis: the novel metric was more strongly aligned than the multi-linear regression framework (Z(198) = -11.564, p < 0.001) and the raw connectomic nodal correlation approach (Z(198) = -10.724, p < 0.001), but the previously-implemented structural manifold approach was more strongly aligned than the novel metric  (Z(198) = -12.242, p < 0.001). This suggests that our novel metric exhibits the expected spatial distribution of structure-function coupling, and the manifold approach more accurately recapitulates the sensorimotor-association axis than approaches based on raw connectomic measures”.

We also added the following to the legend of Figure 4 on page 15:

“d. The inset Spearman correlation plot of the 4 coupling measures shows moderate-to-strong correlations (p_spin < 0.005 for all spatial correlations). The accompanying lollypop plot shows the alignment between the sensorimotor-to-association axis and each of the 4 coupling measures, with the novel measure coloured in light purple (p_spin < 0.007 for all spatial correlations)”. 

Prediction vs. Association Analysis: The term “prediction” is used throughout the manuscript to describe what appear to be in-sample association tests. This terminology may be misleading, as prediction generally implies an out-of-sample evaluation where models trained on a subset of data are tested on a separate, unseen dataset. If the goal of the analyses is to assess associations rather than make true predictions, I recommend refraining from the term “prediction” and instead clarifying the nature of the analysis. Alternatively, if prediction is indeed the intended aim (which would be more compelling), I suggest conducting the evaluations using a k-fold cross-validation framework. This would involve training the Generalized Additive Mixed Models (GAMMs) on a portion of the data and training their predictive accuracy on a held-out sample (i.e. different individuals). Additionally, the current design appears to focus on predicting SC-FC coupling using cognitive or pathological dimensions. This is contrary to the more conventional approach of predicting behavioural or pathological outcomes from brain markers like coupling. Could the authors clarify why this reverse direction of analysis was chosen? Understanding this choice is crucial, as it impacts the interpretation and potential implications of the findings. 

We have replaced “prediction” with “association” across the manuscript. However, for analyses corresponding to Figure 5, which we believe to be the most compelling, we conducted a stratified 5-fold cross-validation procedure, outlined below, repeated 100 times to account for random variation in the train-test splits. To assess whether prediction accuracy in the test splits was significantly greater than chance, we compared our results to those derived from a null dataset in which cognitive factor 2 scores had been permuted across participants. To account for the time-series element and block design of our data, in that some participants had 2 or more observations, we permuted entire participant blocks of cognitive factor 2 scores, keeping all other variables, including covariates, the same. Included in our manuscript are methodological details and results pertaining to this procedure. Specifically, the following has been added to the Results (Page 16, Line 758):

“To examine the predictive value of the second cognitive factor for global and network-level structure-function coupling, operationalised as a Spearman rank correlation coefficient, we implemented a stratified 5-fold crossvalidation framework, and predictive accuracy compared with that of a null data frame with cognitive factor 2 scores permuted across participant blocks (see ‘GAMM cross-validation’ in the Methods). This procedure was repeated 100 times to account for randomness in the train-test splits, using the same model specification as above. Therefore, for each of the 5 network partitions in which an interaction between the second cognitive factor and age was a significant predictor of structure-function coupling (global, visual, somato-motor, dorsal attention, and default-mode), we conducted a Welch’s independent-sample t-test to compare 500 empirical prediction accuracies with 500 null prediction accuracies. Across all 5 network partitions, predictive accuracy of coupling was significantly higher than that of models trained on permuted cognitive factor 2 scores (all p < 0.001). We observed the largest difference between empirical (M = 0.029, SD = 0.076) and null (M = -0.052, SD = 0.087) prediction accuracy in the somato-motor network [t (980.791) = 15.748, p < 0.001, Cohen’s d = 0.996], and the smallest difference between empirical (M = 0.080, SD = 0.082) and null (M = 0.047, SD = 0.081) prediction accuracy in the dorsal attention network [t (997.720) = 6.378, p < 0.001, Cohen’s d = 0.403]. To compare relative prediction accuracies, we ordered networks by descending mean accuracy and conducted a series of Welch’s independent sample t-tests, followed by FDR correction (Figure 5X). Prediction accuracy was highest in the default-mode network (M = 0.265, SD = 0.085), two-fold that of global coupling (t(992.824) = 25.777, p_FDR = 5.457 x 10^-112, Cohen’s d = 1.630, M = 0.131, SD = 0.079). Global prediction accuracy was significantly higher than the visual network (t (992.644) = 9.273, p_FDR = 1.462 x 10^-19, Cohen’s d = 0.586, M = 0.083, SD = 0.085), but visual prediction accuracy was not significantly higher than within the dorsal attention network (t (997.064) = 0.554, p_FDR = 0.580, Cohen’s d = 0.035, M = 0.080, SD = 0.082). Finally, prediction accuracy within the dorsal attention network was significantly stronger than that of the somato-motor network [t (991.566) = 10.158, p_FDR = 7.879 x 10^-23, Cohen’s d = 0.642 M = 0.029, SD = 0.076]. Together, this suggests that out-of-sample developmental predictive accuracy for structure-function coupling, using the second cognitive factor, is strongest in the higher-order default-mode network, and lowest in the lower-order somatosensory network”. 

We have added a separate section for GAMM cross-validation in the Methods (Page 27, Line 1361):

GAMM cross-validation

“We implemented a 5-fold cross validation procedure, stratified by dataset (2 levels: CALM or NKI). All observations from any given participant were assigned to either the testing or training fold, to prevent data leakage, and the cross-validation procedure was repeated 100 times, to account for randomness in data splits. The outcome was predicted global or network-level structure-function coupling across all test splits, operationalised as the Spearman rank correlation coefficient. To assess whether prediction accuracy exceeded chance, we compared empirical prediction accuracy with that of GAMMs trained and tested on null data in which cognitive factor 2 scores were permuted across subjects. The number of observations formed 3 exchangeability blocks (N = 320 with one observation, N = 105 with two observations, and N = 33 with three observations), whereby scores from a participant with two observations were replaced by scores from another participant with two observations, with participant-level scores kept together, and so on for all numbers of observations. We compared empirical and null prediction accuracies using independent sample t-tests as, although the same participants were examined, the shuffling meant that the relative ordering of participants within both distributions was not preserved. For parallelisation and better stability when estimating models fit on permuted data, we used the bam function from the mgcv R package (Wood, 2017)”. 

We also added a justification for why we predicted coupling using behaviour or psychopathology, rather than vice versa (Page 27, Line 1349):

“When using our GAMMs to test for the relationship between cognition and psychopathology and our coupling metrics, we opted to predict structure-function coupling using cognitive or psychopathological dimensions, rather than vice versa, to minimise multiple comparisons. In the current framework, we corrected for 8 multiple comparisons within each domain. This would have increased to 16 multiple comparison corrections for predicting two cognitive dimensions using network-level coupling, and 24 multiple comparison corrections for predicting three psychopathology dimensions. Incorporating multiple networks as predictors within the same regression framework introduces collinearity, whilst the behavioural dimensions were orthogonal: for example, coupling is strongly correlated between the somato-motor and ventral attention networks (r_s = 0.721), between the default-mode and frontoparietal networks (r_s = 0.670), and between the dorsal attention and fronto-parietal networks (r_s = 0.650)”. 

Finally, we noticed a rounding error in the ages of the data frame containing the structure-function coupling values and the cognitive/psychopathology dimensions. We rectified this and replaced the GAMM results, which largely remained the same. 

In typical applications of diffusion map embedding, sparsification (e.g., retaining only the top 10  of the strongest connections) is often employed at the vertex-level resolution to ensure computational feasibility. However, since the present study performs the embedding at the level of 200 brain regions (a considerably coarser resolution), this step may not be necessary or justifiable. Specifically, for FC, it might be more appropriate to retain all positive connections rather than applying sparsification, which could inadvertently eliminate valuable information about lower-strength connections. Whereas for SC, as the values are strictly non-negative, retaining all connections should be feasible and would provide a more complete representation of the structural connectivity patterns. Given this, it would be helpful if the authors could clarify why they chose to include sparsification despite the coarser regional resolution, and whether they considered this alternative approach (using all available positive connections for FC and all non-zero values for SC). It would be interesting if the authors could provide their thoughts on whether the decision to run evaluations at the resolution of brain regions could itself impact the functional and structural manifolds, their alteration with age, and or their stability (in contrast to Dong et al. which tested alterations in highresolution gradients).

This is another great point. We could retain all connections, but we usually implement some form of sparsification to reduce noise, particularly in the case of functional connectivity. But we nonetheless agree with the reviewer’s point. We should check what impact this is having on the analysis. In brief, we found minimal effects of thresholding, suggesting that the strongest connections are driving the gradient (Page 7, Line 304):

“To assess the effect of sparsity on the derived gradients, we examined group-level structural (N = 222) and functional (N = 213) connectomes from the baseline session of NKI. The first three functional connectivity gradients derived using the full connectivity matrix (density = 92%) were highly consistent with those obtained from retaining the strongest 10% of connections in each row (r₁ = 0.999, r₂ = 0.998, r₃ < 0.999, all p < 0.001). Likewise, the first three communicability gradients derived from retaining all streamline counts (density = 83%) were almost identical to those obtained from 10% row-wise thresholding (r₁ = 0.994, r₂ = 0.963, r₃ = 0.955, all p < 0.001). This suggests that the reported gradients are driven by the strongest or most consistent connections within the connectomes, with minimal additional information provided by weaker connections. In terms of functional connectivity, such consistency reinforces past work demonstrating that the sensorimotor-toassociation axis, the major axis within the principal functional connectivity gradient, emerges across both the top- and bottom-ranked functional connections (Nenning et al., 2023)”.

Furthermore, we appreciate the nudge to share our thoughts on whether the difference between vertex versus nodal metrics could be important here, particularly regarding thresholds. To combine this point with R2’s recommendation to expand the Discussion, we have added the following paragraph (Page 19, Line 861): 

“We consider the role of thresholding, cortical resolution, and head motion as avenues to reconcile the present results with select reports in the literature (Dong et al., 2021; Xia et al., 2022). We would suggest that thresholding has a greater effect on vertex-level data, rather than parcel-level. For example, a recent study revealed that the emergence of principal vertex-level functional connectivity gradients in childhood and adolescence are indeed threshold-dependent (Dong et al., 2024). Specifically, the characteristic unimodal organisation for children and transmodal organisation for adolescents only emerged at the 90% threshold: a 95% threshold produced a unimodal organisation in both groups, whilst an 85% threshold produced a transmodal organisation in both groups. Put simply, the ‘swapping’ of gradient orders only occurs at certain thresholds. Furthermore, our results are not necessarily contradictory to this prior report (Dong et al., 2021): developmental changes in high-resolution gradients may be supported by a stable low-dimensional coarse manifold. Indeed, our decision to use parcellated connectomes was partly driven by recent work which demonstrated that vertex-level functional gradients may be derived using biologically-plausible but random data with sufficient spatial smoothing, whilst this effect is minimal at coarser resolutions (Watson & Andrews, 2023). We observed a gradual increase in the variance of individual connectomes accounted for by the principal functional connectivity gradient in the referred subset of CALM, in line with prior vertex-level work demonstrating a gradual emergence of the sensorimotor-association axis as the principal axis of connectivity (Xia et al., 2022), as opposed to a sudden shift. It is also possible that vertex-level data is more prone to motion artefacts in the context of developmental work. Transitioning from vertex-level to parcel-level data involves smoothing over short-range connectivity, thus greater variability in short-range connectivity can be observed in vertex-level data. However, motion artefacts are known to increase short-range connectivity and decrease long-range connectivity, mimicking developmental changes (Satterthwaite et al., 2013). Thus, whilst vertexlevel data offers greater spatial resolution in representation of short-range connectivity relative to parcel-level data, it is possible that this may come at the cost of making our estimates of the gradients more prone to motion”.

Evaluating the consistency of gradients across development: the results shown in Figure 1e are used as evidence suggesting that gradients are consistent across ages. However, I believe additional analyses are required to identify potential sources of the observed inconsistency compared to previous works. The claim that the principal gradient explains a similar degree of variance across ages does not necessarily imply that the spatial structure remains the same. The observed variance explanation is hence not enough to ascertain inconsistency with findings from Dong et al., as the spatial configuration of gradients may still change over time. I suggest the following additional analyses to strengthen this claim. Alignment to group-level gradients: Assess how much of the variance in individual FC matrices is explained by each of the group-level gradients (G1, G2, and G3, for both FC and SC). This analysis could be visualized similarly to Figure 1e, with age on the x-axis and variance explained on the y-axis. If the explained variance varies as a function of age, it may indicate that the gradients are not as consistent as currently suggested. 

This is another great suggestion. In the additional analyses above (new group-level analyses and unrotated gradient analyses) we rule-out a couple of the potential causes of the different developmental trends we observe in our data – namely the stability of the gradients over time. The suggested additional analysis is a great idea, and we have implemented it as follows (Page 8, Line 363):

“To evaluate the consistency of gradients across development, across baseline participants with functional connectomes from the referred CALM cohort (N = 177), we calculated the proportion of variance in individuallevel connectomes accounted for by group-level functional gradients. Specifically, we calculated the proportion of variance in an adjacency matrix A accounted for by the vector v_i as the fraction of the square of the scalar projection of v_i onto A, over the Frobenius norm of A. Using a generalised linear model, we then tested whether the proportion of variance explained varies systematically with age, controlling for sex and headmotion. The variance in individual-level functional connectomes accounted for by the group-level principal functional gradient gradually increased with development (β= 0.111, 95% CI = [0.022, 0.199], p = 1.452 x 10^-2, Cohen’s d = 0.367), as shown in Figure 1g, and decreased with higher head motion ( β = -10.041, 95% CI = [12.379, -7.702], p = 3.900 x 10^-17), with no effect of sex (β= 0.071, 95% CI = [-0.380, 0.523], p = 0.757). We observed no developmental effects on the variance explained by the second (r_s = 0.112, p = 0.139) or third (r_s = 0.053, p = 0.482) group-level functional gradient. When repeated with the baseline functional connectivity for NKI (N = 213), we observed no developmental effects (β = 0.097, 95% CI = [-0.035, 0.228], p = 0.150) on the variance explained by the principal functional gradient after accounting for motion (β= -3.376, 95% CI = [8.281, 1.528], p = 0.177) and sex (β = -0.368, 95% CI = [-1.078, 0.342], p = 0.309). However, we observed significant developmental correlations between age and variance (r_s = 0.137, p = 0.046) explained before accounting for head motion and sex. We observed no developmental effects on the variance explained by the second functional gradient (r_s = -0.066, p = 0.338), but a weak negative developmental effect on the variance explained by the third functional gradient (r_s = -0.189, p = 0.006). Note, however, the magnitude of the variance accounted for by the third functional gradient was very small (all < 1%). When applied to communicability matrices in CALM, the proportion of variance accounted for by the group-level communicability gradient was negligible (all < 1%), precluding analysis of developmental change”. 

“To further probe the consistency of gradients across development, we examined developmental changes in the standard deviation of gradient values, corresponding to heterogeneity, following prior work examining morphological (He et al., 2025) and functional connectivity gradients (Xia et al., 2022). Using a series of generalised linear models within the baseline referred subset of CALM, correcting for head motion and sex, we found that gradient variation for the principal functional gradient increased across development (= 0.219, 95% CI = [0.091, 0.347], p = 0.001, Cohen’s d = 0.504), indicating greater heterogeneity (Figure 1h), whilst gradient variation for the principal communicability gradient decreased across development (β = -0.154, 95% CI = [-0.267, -0.040], p = 0.008, Cohen’s d = -0.301), indicating greater homogeneity (Figure 1h). Note, a paired t-test on the 173 common participants demonstrated a significant effect of modality on gradient variability (t(172) = -56.639, p = 3.663 x 10^-113), such that the mean variability of communicability gradients (M = 0.033, SD = 0.001) was less than half that of functional connectivity (M = 0.076, SD = 0.010). Together, this suggests that principal functional connectivity and communicability gradients are established early in childhood and display age-related refinement, but not replacement”. 

The Issue of Abstraction and Benefits of the Gradient-Based View: The manuscript interprets the eccentricity findings as reflecting changes along the segregation-integration spectrum. Given this, it is unclear why a more straightforward analysis using established graph-theory metrics of segregationintegration was not pursued instead. Mapping gradients and computing eccentricity adds layers of abstraction and complexity. If similar interpretations can be derived directly from simpler graph metrics, what additional insights does the gradient-based framework offer? While the manuscript argues that this approach provides “a more unifying account of cortical reorganization”, it is not evident why this abstraction is necessary or advantageous over traditional graph metrics. Clarifying these benefits would strengthen the rationale for using this method. 

This is a great point, and something we spent quite a bit of time considering when designing the analysis. The central goal of our project was to identify gradients of brain organisation across different datasets and modalities and then test how the organisational principles of those modalities align. In other words, how do structural and functional ‘spaces’ intersect, and does this vary across the cortex? That for us was the primary motivation for operationalising organisation as nodal location within a low-dimensional manifold space (Bethlehem et al., 2020; Gale et al., 2022; Park et al., 2021), using a simple composite measure to achieve compression, rather than as a series of graph metrics. The reason we subsequently calculated those graph metrics and tested for their association was simply to help us interpret what eccentricity within that lowdimensional space means. Manifold eccentricity was moderately positively correlated to graph-theory metrics of integration, leaving a substantial portion of variance unaccounted for, but that association we think is nonetheless helpful for readers trying to interpret eccentricity. However, since ME tells us about the relative position of a node in that low-dimensional space, it is also likely capturing elements of multiple graph theory measures. Following the Reviewer’s question, this is something we decided to test. Specifically, using 4 measures of segregation, including two new metrics requested by the Reviewer in a minor point (weighted clustering coefficient and normalized degree centrality), we conducted a dominance analysis (Budescu, 1993) with normalized manifold eccentricity of the group-level referred CALM structural connectome. We also detail the use of gradient measures in developmental contexts, and how they can be complementary to traditional graph theory metrics. 

We have added the following to the Results section (Page 10, Lines 472 onwards): 

“To further contextualise manifold eccentricity in terms of integration and segregation beyond simple correlations, we conducted a multivariate dominance analysis (Budescu, 1993) of four graph theory metrics of segregation as predictors of nodal normalized manifold eccentricity within the group-level referred CALM structural and functional connectomes (Figure 2c). A dominance analysis assesses the relative importance of each predictor in a multilinear regression framework by fitting 2ⁿ – 1 models (where n is the number of predictors) and calculating the relative increase in adjusted R2 caused by adding each predictor to the model across both main effects and interactions. A multilinear regression model including weighted clustering coefficient, within-module degree Z-score, participation coefficient and normalized degree centrality accounted for 59% of variance in nodal manifold eccentricity in the group-level CALM structural connectome. Withinmodule degree Z score was the most important predictor (40.31% dominance), almost twice that of the participation coefficient (24.03% dominance) and normalized degree centrality (24.05% dominance) which made roughly equal contributions. The least important predictor was the weighted clustering coefficient (11.62% dominance). When the same approach was applied for the group-level referred CALM functional connectome, the 4 predictors accounted for 52% variability. However, in contrast to the structural connectome, functional manifold eccentricity seemed to incorporate the same graph theory metrics in different proportions. Normalized degree centrality was the most important predictor (47.41% dominance), followed by withinmodule degree Z-score (24.27%), and then the participation coefficient (15.57%) and weighted clustering coefficient (12.76%) which made approximately equal contributions. Thus, whilst structural manifold eccentricity was dominated most by within-module degree Z-score and least by the weighted clustering coefficient, functional manifold eccentricity was dominated most by normalized degree centrality and least by the weighted clustering coefficient. This suggests that manifold mapping techniques incorporate different aspects of integration dependent on modality. Together, manifold eccentricity acts as a composite measure of segregation, being differentially sensitive to different aspects of segregation, without necessitating a priori specification of graph theory metrics. Further discussion of the value of gradient-based metrics in developmental contexts and as a supplement to traditional graph theory analyses is provided in the ‘Manifold Eccentricity’ methodology sub-section”. 

We added further justification to the manifold eccentricity Methods subsection (Page 26, line 1283):

“Gradient-based measures hold value in developmental contexts, above and beyond traditional graph theory metrics: within a sample of over 600 cognitively-healthy adults aged between 18 and 88 years old, sensitivity of gradient-based within-network functional dispersion to age were stronger and more consistent across networks compared to segregation (Bethlehem et al., 2020). In the context of microstructural profile covariance, modules resolved by Louvain community detection occupied distinct positions across the principal two gradients, suggesting that gradients offer a way to meaningfully order discrete graph theory analyses (Paquola et al., 2019)”. 

We added the following to the Introduction section outlining the application of gradients as cortex-wide coordinate systems (Page 3, Line 121):

“Using the gradient-based approach as a compression tool, thus forgoing the need to specify singular graph theory metrics a priori, we operationalised individual variability in low-dimensional manifolds as eccentricity (Gale et al., 2022; Park et al., 2021). Crucially, such gradients appear to be useful predictors of phenotypic variation, exceeding edge-level connectomics. For example, in the case of functional connectivity gradients, their predictive ability for externalizing symptoms and general cognition in neurotypical adults surpassed that of edge-level connectome-based predictive modelling (Hong et al., 2020), suggesting that capturing lowdimensional manifolds may be particularly powerful biomarkers of psychopathology and cognition”. 

We also added the following to the Discussion section (Page 18, Line 839):

“By capitalising on manifold eccentricity as a composite measure of segregation across development, we build upon an emerging literature pioneering gradients as a method to establish underlying principles of structural (Paquola et al., 2020; Park et al., 2021) and functional (Dong et al., 2021; Margulies et al., 2016; Xia et al., 2022) brain development without a priori specification of specific graph theory metrics of interest”. 

It is unclear whether the statistical tests finding significant dataset effects are capturing effects of neurotypical vs. Neurodivergent, or simply different scanners/sites. Could the neurotypical portion of CALM also be added to distinguish between these two sources of variability affecting dataset effects (i.e. ideally separating this to the effect of site vs. neurotypicality would better distinguish the effect of neurodivergence).

At a group-level, differences in the gradients between the two cohorts are very minor. Indeed, in the manuscript we describe these gradients as being seemingly ‘universal’. But we agree that we should test whether we can directly attribute any simple main effects of ‘dataset’ are resulting from the different site or the phenotype of the participants. The neurotypical portion of CALM (collected at the same site on the same scanner) helped us show that any minor differences in the gradient alignments is likely due to the site/scanner differences rather than the phenotype of the participants. We took the same approach for testing the simple main effects of dataset on manifold eccentricity. To better parse neurotypicality and site effects at an individual-level, we conducted a series of sensitivity analyses. First, in response to the reviewer’s earlier comment, we conducted a series of nodal generalized linear models for communicability and FC gradients derived from neurotypical and neurodivergent portions of CALM, alongside NKI, and tested for an effect of neurotypicality above and beyond scanner. As at the group level, having those additional scans on a ‘comparison’ sample for CALM is very helpful in teasing apart these effects. We find that neurotypicality affects communicability gradient expression to a greater degree than functional connectivity. We visualised these results and added them to Figure 1. Second, we used the same approach but for manifold eccentricity. Again, we demonstrate greater sensitivity of neurotypicality to communicability at a global-level, but we cannot pin these effects down to specific networks because the effects do not survive the necessary multiple comparison correction. We have added these analyses to the manuscript (Page 13, Line 583): 

“Much as with the gradients themselves, we suspected that much of the simple main effect of dataset could reflect the scanner / site, rather than the difference in phenotype. Again, we drew upon the CALM comparison children to help us disentangle these two explanations. As a sensitivity analysis to parse effects of neurotypicality and dataset on manifold eccentricity, we conducted a series of generalized linear models predicting mean global and network-level manifold eccentricity, for each modality. We did this across all the baseline data (i.e. including the neurotypical comparison sample for CALM) using neurotypicality (2 levels: neurodivergent or neurotypical), site (2 levels: CALM or NKI), sex, head motion, and age at scan (Figure 3X). We restricted our analysis to baseline scans to create more equally-balanced groups. In terms of structural manifold eccentricity (N = 313 neurotypical, N = 311 neurodivergent), we observed higher manifold eccentricity in the neurodivergent participants at a global level (β = 0.090, p = 0.019, Cohen’s d = 0.188) but the individual network level effects did not survive the multiple comparison correction necessary for looking across all seven networks, with the default-mode network being the strongest (β = 0.135, p = 0.027, p_FDR = 0.109, Cohen’s d = 0.177). There was no significant effect of neurodiversity on functional manifold eccentricity (N = 292 neurotypical and N = 177 neurodivergent). This suggests that neurodiversity is significantly associated with structural manifold eccentricity, over and above differences in site, but we cannot distinguish these effects reliably in the functional manifold data”. 

Third, we removed the Scheirer-Ray-Hare test from the results for two reasons. First, its initial implementation did not account for repeated measures, and therefore non-independence between observations, as the same participants may have contributed both structural and functional data. Second, if we wanted to repeat this analysis in CALM using the referred and control portions, a significant difference in group size existed, which may affect the measures of variability. Specifically, for baseline CALM, 311 referred and 91 control participants contributed SC data, whilst 177 referred and 79 control participants contributed FC data. We believe that the ‘cleanest’ parsing of dataset and site for effects of eccentricity is achieved using the GLMs in Figure 3. 

We observed no significant effect of neurodivergence on the magnitude of structure-function coupling across development, and have added the following text (Page 14, Line 632):

“To parse effects of neurotypicality and dataset on structure-function coupling, we conducted a series of generalized linear models predicting mean global and network-level coupling using neurotypicality, site, sex, head motion, and age at scan, at baseline (N = 77 CALM neurotypical, N = 173 CALM neurodivergent, and N = 170 NKI). However, we found no significant effects of neurotypicality on structure-function coupling across development”. 

Since we demonstrated no significant effects of neurotypicality on structure-function coupling magnitude across development, but found differential dataset-specific effects of age on coupling development, we added the following sentence at the end of the coupling trajectory results sub-section (Page 14, line 664):

“Together, these effects demonstrate that whilst the magnitude of structure-function coupling appears not to be sensitive to neurodevelopmental phenotype, its development with age is, particularly in higher-order association networks, with developmental change being reduced in the neurodivergent sample”.  

Figure 1.c: A non-parametric permutation test (e.g. Mann-Whitney U test) could quantitatively identify regions with significant group differences in nodal gradient values, providing additional support for the qualitative findings.

This is a great idea. To examine the effect of referral status on nodal gradient values, whilst controlling for covariates (head motion and sex), we conducted a series of generalised linear models. We opted for this instead of a Mann-Whitney U test, as the former tests for differences in distributions, whilst the direction of the t-statistic for referral status from the GLM would allow us to specify the magnitude and direction of differences in nodal gradient values between the two groups. Again, we conducted this in CALM (referred vs control), at an individual-level, as downstream analyses suggested a main effect of dataset (which is reflected in the highly-similar group-level referred and control CALM gradients). We have updated the Results section with the following text (Page 6, Line 283):

“To examine the effect of referral status on participant-level nodal gradient values in CALM, we conducted a series of generalized linear models controlling for head motion, sex and age at scan (Figure 1d). We restricted our analyses to baseline scans to reduce the difference in sample size for the referred (311 communicability and 177 functional gradients, respectively) and control participants (91 communicability and 79 functional gradients, respectively), and to the principal gradients. For communicability, 42 regions showed a significant effect (p < 0.05) of neurodivergence before FDR correction, with 9 post FDR correction. 8 of these 9 regions had negative t-statistics, suggesting a reduced nodal gradient value and representation in the neurodivergent children, encompassing both lower-order somatosensory cortices alongside higher-order fronto-parietal and default-mode networks. The largest reductions were observed within the prefrontal cortices of the defaultmode network (t = -3.992, p = 6.600 x 10^-5, p_FDR = 0.013, Cohen’s d = -0.476), the left orbitofrontal cortex of the limbic network (t = -3.710, p = 2.070 x 10^-4, p_FDR = 0.020, Cohen’s d = -0.442) and right somato-motor cortex (t = -3.612, p = 3.040 x 10^-4, p_FDR = 0.020, Cohen’s d = -0.431). The right visual cortex was the only exception, with stronger gradient representation within the neurotypical cohort (t = 3.071, p = 0.002, p_FDR = 0.048, Cohen’s d = 0.366). For functional connectivity, comparatively fewer regions exhibited a significant effect (p < 0.05) of neurotypicality, with 34 regions prior to FDR correction and 1 post. Significantly stronger gradient representation was observed in neurotypical children within the right precentral ventral division of the defaultmode network (t = 3.930, p = 8.500 x 10^-5, p_FDR = 0.017, Cohen’s d = 0.532). Together, this suggests that the strongest and most robust effects of neurodivergence are observed within gradients of communicability, rather than functional connectivity, where alterations in both affect higher-order associative regions”. 

In the harmonization methodology, it is mentioned that “if harmonisation was successful, we’d expect any significant effects of scanner type before harmonisation to be non-significant after harmonisation”. However, given that there were no significant effects before harmonization, the results reported do not help in evaluating the quality of harmonization.

We agree with the Reviewer, and have removed the post-harmonisation GLMs, and instead stating that there were no significant effects of scanner type before harmonization. 

Figure 3: It would be helpful to include a plot showing the GAMM predictions versus real observations of eccentricity (x-axis: predictions, y-axis: actual values). 

To plot the GAMM-predicted smooth effects of age, which we used for visualisation purposes only, we used the get_predictions function from the itsadug R package. This creates model predictions using the median value of nuisance covariates. Thus, whilst we specified the entire age range, the function automatically chooses the median of head motion, alongside controlling for sex (default level: male) and, for each dataset-specific trajectory. Since the gamm4 package separates the fitted model into a gam and linear mixed effects model (which accounts for participant ID as a random effect), and the get_predictions function only uses gam, random effects are not modelled in the predicted smooths. Therefore, any discrepancy between the observed and predicted manifold eccentricity values is likely due to sensitivity to default choices of covariates other than age, or random effects. To prevent Figure 3 being too over-crowded, we opted to not include the predictions: these were strongly correlated with real structural manifold data, but less for functional manifold data especially where significant developmental change was absent.

The 30mm threshold for filtering short streamlines in tractography is uncommon. What is the rationale for using such a large threshold, given the potential exclusion of many short-range association fibres?

A minimum length of 30mm was the default for the MRtrix3 reconstruction workflow, and something we have previously used. In a previous project, we systematically varied the minimum fibre length and found that this had minimal impact on network organisation (e.g. Mousley et al. 2025). However, we accept that short-range association fibres may have been excluded and have included this in the Discussion as a methodological limitation, alongside our predictions for how the gradients and structure-function coupling may’ve been altered had we included such fibres (Page 20, Line 955):

“A potential methodological limitation in the construction of structural connectomes was the 30mm tract length threshold which, despite being the QSIprep reconstruction default (Cieslak et al., 2021), may have potentially excluded short-range association fibres. This is pertinent as tracts of different lengths exhibit unique distributions across the cortex and functional roles (Bajada et al., 2019) : short-range connections occur throughout the cortex but peak within primary areas, including the primary visual, somato-motor, auditory, and para-hippocampal cortices, and are thought to dominate lower-order sensorimotor functional resting-state networks, whilst long-range connections are most abundant in tertiary association areas and are recruited alongside tracts of varying lengths within higher-order functional resting-state networks. Therefore, inclusion of short-range association fibres may have resulted in a relative increase in representation of lower-order primary areas and functional networks. On the other hand, we also note the potential misinterpretation of short-range fibres: they may be unreliably distinguished from null models in which tractography is restricted by cortical gyri only (Bajada et al., 2019). Further, prior (neonatal) work has demonstrated that the order of connectivity of regions and topological fingerprints are consistent across varying streamline thresholds (Mousley et al., 2025), suggesting minimal impact”. 

Given the spatial smoothing of fMRI data (6mm FWHM), it would be beneficial to apply connectome spatial smoothing to structural connectivity measures for consistent spatial smoothness.

This is an interesting suggestion but given we are looking at structural communicability within a parcellated network, we are not sure that it would make any difference. The data structural data are already very smooth. Nonetheless we have added the following text to the Discussion (Page 20, Line 968): 

“Given the spatial smoothing applied to the functional connectivity data, and examining its correspondence to streamline-count connectomes through structure-function coupling, applying the equivalent smoothing to structural connectomes may improve the reliability of inference, and subsequent sensitivity to cognition and psychopathology. Connectome spatial smoothing involves applying a smoothing kernel to the two streamline endpoints, whereby variations in smoothing kernels are selected to optimise the trade-off between subjectlevel reliability and identifiability, thus increasing the signal-to-noise ratio and the reliability of statistical inferences of brain-behaviour relationships (Mansour et al., 2022). However, we note that such smoothing is more effective for high-resolution connectomes, rather than parcel-level, and so have only made a modest improvement (Mansour et al., 2022)”.

Why was harmonization performed only within the CALM dataset and not across both CALM and NKI datasets? What was the rationale for this decision?

We thought about this very carefully. Harmonization aims to remove scanner or site effects, whilst retaining the crucial characteristics of interest. Our capacity to retain those characteristics is entirely dependent on them being *fully* captured by covariates, which are then incorporated into the harmonization process. Even with the best set of measures, the idea that we can fully capture ‘neurodivergence’ and thus preserve it in the harmonisation process is dubious. Indeed, across CALM and NKI there are limited number of common measures (i.e. not the best set of common measures), and thus we are limited in our ability to fully capture the neurodivergence with covariates. So, we worried that if we put these two very different datasets into the harmonisation process we would essentially eliminate the interesting differences between the datasets. We have added this text to the harmonization section of the Methods (Page 24, Line 1225):

“Harmonization aims to retain key characteristics of interest whilst removing scanner or site effects. However, the site effects in the current study are confounded with neurodivergence, and it is unlikely that neurodivergence may be captured fully using common covariates across CALM and NKI. Therefore, to preserve variation in neurodivergence, whilst reducing scanner effects, we harmonized within the CALM dataset only”. 

The exclusion of subcortical areas from connectivity analyses is not justified. 

This is a good point. We used the Schaefer atlas because we had previously used this to derive both functional and structural connectomes, but we agree that it would have been good to include subcortical areas (Page 20, Line 977). 

“A potential limitation of our study was the exclusion of subcortical regions. However, prior work has shed light on the role of subcortical connectivity in structural and functional gradients, respectively, of neurotypical populations of children and adolescents (Park et al., 2021; Xia et al., 2022). For example, in the context of the primary-to-transmodal and sensorimotor-to-visual functional connectivity gradients, the mean gradient scores within subcortical networks were demonstrated to be relatively stable across childhood and adolescence (Xia et al., 2022). In the context of structural connectivity gradients derived from streamline counts, which we demonstrated were highly consistent with those derived from communicability, subcortical structural manifolds weighted by their cortical connectivity were anchored by the caudate and thalamus at one pole, and by the hippocampus and nucleus accumbens at the opposite pole, with significant age-related manifold expansion within the caudate and thalamus (Park et al., 2021)”. 

In the KNN imputation method, were uniform weights used, or was an inverse distance weighting applied?

Uniform weights were used, and we have updated the manuscript appropriately.

The manuscript should clarify from the outset that the reported sample size (N) includes multiple longitudinal observations from the same individuals and does not reflect the number of unique participants.

We have rectified the Abstract (Page 2, Line 64) and Introduction (Page 3, Line 138):

“We charted the organisational variability of structural (610 participants, N = 390 with one observation, N = 163 with two observations, and N = 57 with three) and functional (512 participants, N = 340 with one observation, N = 128 with two observations, and N = 44 with three)”.

The term “structural gradients” is ambiguous in the introduction. Clarify that these gradients were computed from structural and functional connectivity matrices, not from other structural features (e.g. cortical thickness).

We have clarified this in the Introduction (Page 3, Line 134):

“Applying diffusion-map embedding as an unsupervised machine-learning technique onto matrices of communicability (from streamline SIFT2-weighted fibre bundle capacity) and functional connectivity, we derived gradients of structural and functional brain organisation in children and adolescents…”

Page 5: The sentence, “we calculated the normalized angle of each structural and functional connectome to derive symmetric affinity matrices” is unclear and needs clarification.

We have clarified this within the second paragraph of the Results section (Page 4, Line 185):

“To capture inter-nodal similarity in connectivity, using a normalised angle kernel, we derived individual symmetric affinity matrices from the left and right hemispheres of each communicability and functional connectivity matrix. Varying kernels capture different but highly-related aspects of inter-nodal similarity, such as correlation coefficients, Gaussian kernels, and cosine similarity. Diffusion-map embedding is then applied on the affinity matrices to derive gradients of cortical organisation”. 

Figure 1.a: “Affine A” likely refers to the affinity matrix. The term “affine” may be confusing; consider using a clearer label. It would also help to add descriptive labels for rows and columns (e.g. region x region).

Thank you for this suggestion! We have replaced each of the labels with “pairwise similarity”. We also labelled the rows and columns as regions.

Figure 1.d: Are the cross-group differences statistically significant? If so, please indicate this in the figure.

We have added the results of a series of linear mixed effects models to the legend of Figure 1 (Page 6, line 252):

“indicates a significant effect of dataset (p < 0.05) on variance explained within a linear mixed effects model controlling for head motion, sex, and age at scan”.

The sentence “whose connectomes were successfully thresholded” in the methods is unclear. What does “successfully thresholded” mean? Additionally, this seems to be the first mention of the Schaefer 100 and Brainnetome atlas; clarify where these parcellations are used. 

We have amended the Methodology section (Page 23, Line 1138):

“For each participant, we retained the strongest 10% of connections per row, thus creating fully connected networks required for building affinity matrices. We excluded any connectomes in which such thresholding was not possible due to insufficient non-zero row values. To further ensure accuracy in connectome reconstruction, we excluded any participants whose connectomes failed thresholding in two alternative parcellations: the 100node Schaefer 7-network (Schaefer et al., 2018) and Brainnetome 246-node (Fan et al., 2016) parcellations, respectively”. 

We have also specified the use of the Schaefer 200-node parcellation in the first sentence on the second Results paragraph.

The use of “streamline counts” is misleading, as the method uses SIFT2-weighted fibre bundle capacity rather than raw streamline counts. It would be better to refer to this measure as “SIFT2-weighted fibre bundle capacity” or “FBC”.

We replaced all instances of “streamline counts” with “SIFT2-weighted fibre bundle capacity” as appropriate.

Figure 2.c: Consider adding plots showing changes in eccentricity against (1) degree centrality, and (2) weighted local clustering coefficient. Additionally, a plot showing the relationship between age and mean eccentricity (averaged across nodes) at the individual level would be informative.

We added the correlation between eccentricity and both degree centrality and the weighted local clustering coefficient and included them in our dominance analysis in Figure 2. In terms of the relationship between age and mean (global) eccentricity, these are plotted in Figure 3. 

Figure 2.b: Considering the results of the following sections, it would be interesting to include additional KDE/violin plots to show group differences in the distribution of eccentricity within 7 different functional networks.

As part of our analysis to parse neurotypicality and dataset effects, we tested for group differences in the distribution of structural and functional manifold eccentricity within each of the 7 functional networks in the referred and control portions of CALM and have included instances of significant differences with a coloured arrow to represent the direction of the difference within Figure 3. 

Figure 3: Several panels lack axis labels for x and y axes. Adding these would improve clarity.

To minimise the amount of text in Figure 3, we opted to include labels only for the global-level structural and functional results. However, to aid interpretation, we added a small schematic at the bottom of Figure 3 to represent all axis labels. 

The statement that “differences between datasets only emerged when taking development into account” seems inaccurate. Differences in eccentricity are evident across datasets even before accounting for development (see Fig 2.b and the significance in the Scheirer-Ray-Hare test).

We agree – differences in eccentricity across development and datasets are evident in structural and functional manifold eccentricity, as well as within structure-function coupling. However, effects of neurotypicality were particularly strong for the maturation of structure-function coupling, rather than magnitude. Therefore, we have rephrased this sentence in the Discussion (page 18, line 832):

“Furthermore, group-level structural and functional gradients were highly consistent across datasets, whilst differences between datasets were emphasised when taking development into account, through differing rates of structural and functional manifold expansion, respectively, alongside maturation of structure-function coupling”.

The handling of longitudinal data by adding a random effect for individuals is not clear in the main text. Mentioning this earlier could be helpful. 

We have included this detail in the second sentence of the “developmental trajectories of structural manifold contraction and functional manifold expansion” results sub-section (page 11, line 503):

“We included a random effect for each participant to account for longitudinal data”. 

Figure 4.b: Why were ranks shown instead of actual coefficient of variation values? Consider including a cortical map visualization of the coefficients in the supplementary material.

We visualised the ranks, instead of the actual coefficient of variation (CV) values, due to considerable variability and skew in the magnitude of the CV, ranging from 28.54 (in the right visual network) to 12865.68 (in the parietal portion of the left default-mode network), with a mean of 306.15. If we had visualised the raw CV values, these larger values would’ve been over-represented. We’ve also noticed and rectified an error in the labelling of the colour bar for Figure 4b: the minimum should be most variable (i.e. a rank of 1). To aid contextualisation of the ranks, we have added the following to the Results (page 14, line 626):

“The distribution of cortical coefficients of variation (CV) varied considerably, with the largest CV (in the parietal division of the left default-mode network) being over 400 times that of the smallest (in the right visual network). The distribution of absolute CVs was positively skewed, with a Fisher skewness coefficient g₁ of 7.172, meaning relatively few regions had particularly high inter-individual variability, and highly peaked, with a kurtosis of 54.883, where a normal distribution has a skewness coefficient of 0 and a kurtosis of 3”. 

Reviewer #2 (Public review):

Some differences in developmental trajectories between CALM and NKI (e.g. Figure 4d) are not explained. Are these differences expected, or do they suggest underlying factors that require further investigation?

This is a great point, and we appreciate the push to give a fuller explanation. It is very hard to know whether these effects are expected or not. We certainly don’t know of any other papers that have taken this approach. In response to the reviewer’s point, we decided to run some more analyses to better understand the differences. Having observed stronger age effects on structure-function coupling within the neurotypical NKI dataset, compared to the absent effects in the neurodivergent portion of CALM, we wanted to follow up and test that it really is that coupling is more sensitive to the neurodivergent versus neurotypical difference between CALM and NKI (rather than say, scanner or site effects). In short, we find stronger developmental effects of coupling within the neurotypical portion of CALM, rather than neurodivergent, and have added this to the Results (page 15, line 701):

“To further examine whether a closer correspondence of structure-function coupling with age is associated with neurotypicality, we conducted a follow-up analysis using the additional age-matched neurotypical portion of CALM (N = 77). Given the widespread developmental effects on coupling within the neurotypical NKI sample, compared to the absent effects in the neurodivergent portion of CALM, we would expect strong relationships between age and structure-function coupling with the neurotypical portion of CALM. This is indeed what we found: structure-function coupling showed a linear negative relationship with age globally (F = 16.76, p_FDR < 0.001, adjusted R² = 26.44%), alongside fronto-parietal (F = 9.24, p_FDR = 0.004, adjusted R² = 19.24%), dorsalattention (F = 13.162, p_FDR = 0.001, adjusted R²= 18.14%), ventral attention (F = 11.47, p_FDR  = 0.002, adjusted R²= 22.78), somato-motor (F = 17.37, p_FDR  < 0.001, adjusted R²= 21.92%) and visual (F = 11.79, p_FDR  = 0.002, adjusted R²= 20.81%) networks. Together, this supports our hypothesis that within neurotypical children and adolescents, structure-function coupling decreases with age, showing a stronger effect compared to their neurodivergent counterparts, in tandem with the emergence of higher-order cognition. Thus, whilst the magnitude of structure-function coupling across development appeared insensitive to neurotypicality, its maturation is sensitive. Tentatively, this suggests that neurotypicality is linked to stronger and more consistent maturational development of structure-function coupling, whereby the tethering of functional connectivity to structure across development is adaptive”. 

In conjunction with the Reviewer’s later request to deepen the Discussion, we have included an additional paragraph attempting to explain the differences in neurodevelopmental trajectories of structure-function coupling (Page 19, Line 924):

“Whilst the spatial patterning of structure-function coupling across the cortex has been extensively documented, as explained above, less is known about developmental trajectories of structure-function coupling, or how such trajectories may be altered in those with neurodevelopmental conditions. To our knowledge, only one prior study has examined differences in developmental trajectories of (non-manifold) structure-function coupling in typically-developing children and those with attention-deficit hyperactivity disorder (Soman et al., 2023), one of the most common conditions in the neurodivergent portion of CALM. Namely, using cross-sectional and longitudinal data from children aged between 9 and 14 years old, they demonstrated increased coupling across development in higher-order regions overlapping with the defaultmode, salience, and dorsal attention networks, in children with ADHD, with no significant developmental change in controls, thus encompassing an ectopic developmental trajectory (Di Martino et al., 2014; Soman et al., 2023). Whilst the current work does not focus on any condition, rather the broad mixed population of young people with neurodevelopmental symptoms (including those with and without diagnoses), there are meaningful individual and developmental differences in structure-coupling. Crucially, it is not the case that simply having stronger coupling is desirable. The current work reveals that there are important developmental trajectories in structure-function coupling, suggesting that it undergoes considerable refinement with age. Note that whilst the magnitude of structure-function coupling across development did not differ significantly as a function of neurodivergence, its relationship to age did. Our working hypothesis is that structural connections allow for the ordered integration of functional areas, and the gradual functional modularisation of the developing brain. For instance, those with higher cognitive ability show a stronger refinement of structurefunction coupling across development. Future work in this space needs to better understand not just how structural or functional organisation change with time, but rather how one supports the other”. 

The use of COMBAT may have excluded extreme participants from both datasets, which could explain the lack of correlations found with psychopathology.

COMBAT does not exclude participants from datasets but simply adjusts connectivity estimates. So, the use of COMBAT will not be impacting the links with psychopathology by removing participants. But this did get us thinking. Excluding participants based on high motion may have systematically removed those with high psychopathology scores, meaning incomplete coverage. In other words, we may be under-representing those at the more extreme end of the range, simply because their head-motion levels are higher and thus are more likely to be excluded. We found that despite certain high-motion participants being removed, we still had good coverage of those with high scores and were therefore sensitive within this range. We have added the following to the revised Methods section (Page 26, Line 1338):

“As we removed participants with high motion, this may have overlapped with those with higher psychopathology scores, and thus incomplete coverage. To examine coverage and sensitivity to broad-range psychopathology following quality control, we calculated the Fisher-Pearson skewness statistic g₁ for each of the 6 Conners t-statistic measures and the proportion of youth with a t-statistic equal to or greater than 65, indicating an elevated or very elevated score. Measures of inattention (g₁ = 0.11, 44.20% elevated), hyperactivity/impulsivity (g₁ = 0.48, 36.41% elevated), learning problems (g₁ = 0.45, 37.36% elevated), executive functioning (g₁ = 0.27, 38.16% elevated), aggression (g₁ = 1.65, 15.58% elevated), and peer relations (g₁ = 0.49, 38% elevated) were positively skewed and comprised of at least 15% of children with elevated or very elevated scores, suggesting sufficient coverage of those with extreme scores”. 

There is no discussion of whether the stable patterns of brain organization could result from preprocessing choices or summarizing data to the mean. This should be addressed to rule out methodological artifacts. 

This is a brilliant point. We are necessarily using a very lengthy pipeline, with many design choices to explore structural and functional gradients and their intersection. In conjunction with the Reviewer’s later suggestion to deepen the Discussion, we have added the following paragraph which details the sensitivity analyses we carried out to confirm the observed stable patterns of brain organization (Page 18, Line 863):

“That is, whilst we observed developmental refinement of gradients, in terms of manifold eccentricity, standard deviation, and variance explained, we did not observe replacement. Note, as opposed to calculating gradients based on group data, such as a sliding window approach, which may artificially smooth developmental trends and summarise them to the mean, we used participant-level data throughout. Given the growing application of gradient-based analyses in modelling structural (He et al., 2025; Li et al., 2024) and functional (Dong et al., 2021; Xia et al., 2022) brain development, we hope to provide a blueprint of factors which may affect developmental conclusions drawn from gradient-based frameworks”.

Although imputing missing data was necessary, it would be useful to compare results without imputed data to assess the impact of imputation on findings. 

It is very hard to know the impact of imputation without simply removing those participants with some imputed data. Using a simulation experiment, we expressed the imputation accuracy as the root mean squared error normalized by the range of observable data in each scale. This produced a percentage error margin. We demonstrate that imputation accuracy across all measures is at worst within approximately 11% of the observed data, and at best within approximately 4% of the observed data, and have included the following in the revised Methods section (Page 27, Line 1348):

“Missing data

To avoid a loss of statistical power, we imputed missing data. 27.50% of the sample had one or more missing psychopathology or cognitive measures (equal to 7% of all values), and the data was not missing at random: using a Welch’s t-test, we observed a significant effect of missingness on age [t (264.479) = 3.029, p = 0.003, Cohen’s d = 0.296], whereby children with missing data (M = 12.055 years, SD = 3.272) were younger than those with complete data (M = 12.902 years, SD = 2.685). Using a subset with complete data (N = 456), we randomly sampled 10% of the values in each column with replacement and assigned those as missing, thereby mimicking the proportion of missingness in the entire dataset. We conducted KNN imputation (uniform weights) on the subset with complete data and calculated the imputation accuracy as the root mean squared error normalized by the observed range of each measure. Thus, each measure was assigned a percentage which described the imputation margin of error. Across cognitive measures, imputation was within a 5.40% mean margin of error, with the lowest imputation error in the Trail motor speed task (4.43%) and highest in the Trails number-letter switching task (7.19%). Across psychopathology measures, imputation exhibited a mean 7.81% error margin, with the lowest imputation error in the Conners executive function scale (5.75%) and the highest in the Conners peer relations scale (11.04%). Together, this suggests that imputation was accurate”.

The results section is extensive, with many reports, while the discussion is relatively short and lacks indepth analysis of the findings. Moving some results into the discussion could help balance the sections and provide a deeper interpretation. 

We agree with the Reviewer and appreciate the nudge to expand the Discussion section. We have added 4 sections to the Discussion. The first explores the importance of the default-mode network as a region whose coupling is most consistently predicted by working memory across development and phenotypes, in terms of its underlying anatomy (Paquola et al., 2025) (Page 20, Line 977):

“An emerging theme from our work is the importance of the default-mode network as a region in which structure-function coupling is reliably predicted by working memory across neurodevelopmental phenotypes and datasets during childhood and adolescence. Recent neurotypical adult investigations combining highresolution post-mortem histology, in vivo neuroimaging, and graph-theory analyses have revealed how the underlying neuroanatomy of the default-mode network may support diverse functions (Paquola et al., 2025), and thus exhibit lower structure-function coupling compared to unimodal regions. The default-mode network has distinct neuroanatomy compared to the remaining 6 intrinsic resting-state functional networks (Yeo et al., 2011), containing a distinctive combination of 5 of the 6 von Economo and Koskinas cell types (von Economo & Koskinas, 1925), with an over-representation of heteromodal cortex, and uniquely balancing output across all cortical types. A primary cytoarchitectural axis emerges, beyond which are mosaic-like spatial topographies. The duality of the default-mode network, in terms of its ability to both integrate and be insulated from sensory information, is facilitated by two microarchitecturally distinct subunits anchored at either end of the cytoarchitectural axis (Paquola et al., 2025). Whilst beyond the scope of the current work, structure-function coupling and their predictive value for cognition may also differ across divisions within the default-mode network, particularly given variability in the smoothness and compressibility of cytoarchitectural landscapes across subregions (Paquola et al., 2025)”. 

The second provides a deeper interpretation and contextualisation of greater sensitivity of communicability, rather than functional connectivity, to neurodivergence (Page 19, Lines 907):

“We consider two possible factors to explain the greater sensitivity of neurodivergence to gradients of communicability, rather than functional connectivity. First, functional connectivity is likely more sensitive to head motion than structural-based communicability and suffers from reduced statistical power due to stricter head motion thresholds, alongside greater inter-individual variability. Second, whilst prior work contrasting functional connectivity gradients from neurotypical adults with those with confirmed ASD diagnoses demonstrated vertex-level reductions in the default-mode network in ASD and marginal increases in sensorymotor communities (Hong et al., 2019), indicating a sensitivity of functional connectivity to neurodivergence, important differences remain. Specifically, whilst the vertex-level group-level differences were modest, in line with our work, greater differences emerged when considering step-wise functional connectivity (SFC); in other words, when considering the dynamic transitions of or information flow through the functional hierarchy underlying the static functional connectomes, such that ASD was characterised by initial faster SFC within the unimodal cortices followed by a lack of convergence within the default-mode network (Hong et al., 2019). This emphasis on information flow and dynamic underlying states may point towards greater sensitivity of neurodivergence to structural communicability – a measure directly capturing information flow – than static functional connectivity”. 

The third paragraph situates our work within a broader landscape of reliable brain-behaviour relationships, focusing on the strengths of combining clinical and normative samples to refine our interpretation of the relationship between gradients and cognition, as well as the importance of equifinality in developmental predictive work (Page 20, line 994):

“In an effort to establish more reliable brain-behaviour relationships despite not having the statistical power afforded by large-scale, typically normative, consortia (Rosenberg & Finn, 2022), we demonstrated the development-dependent link between default-mode structure-function coupling and working memory generalised across clinical (CALM) and normative (NKI) samples, across varying MRI acquisition parameters, and harnessing within- and across-participant variation. Such multivariate associations are likely more reliable than their univariate counterparts (Marek et al., 2022), but can be further optimised using task-related fMRI (Rosenberg & Finn, 2022). The consistency, or lack of, of developmental effects across datasets emphasises the importance of validating brain-behaviour relationships in highly diverse samples. Particularly evident in the case of structure-function coupling development, through our use of contrasting samples, is equifinality (Cicchetti & Rogosch, 1996), a key concept in developmental neuroscience: namely, similar ‘endpoints’ of structure-function coupling may be achieved through different initialisations dependent on working memory. 

The fourth paragraph details methodological limitations in response to Reviewer 1’s suggestions to justify the exclusion of subcortical regions and consider the role of spatial smoothing in structural connectome construction as well as the threshold for filtering short streamlines”. 

While the methods are thorough, it is not always clear whether the optimal approaches were chosen for each step, considering the available data. 

In response to Reviewer 1’s concerns, we conducted several sensitivity analyses to evaluate the robustness of our results in terms of procedure. Specifically, we evaluated the impact of thresholding (full or sparse), level of analysis (individual or group gradients), construction of the structural connectome (communicability or fibre bundle capacity), Procrustes rotation (alignment to group-level gradients before Procrustes), tracking the variance explained in individual connectomes by group-level gradients, impact of head motion, and distinguishing between site and neurotypicality effects. All these analyses converged on the same conclusion: whilst we observe some developmental refinement in gradients, we do not observe replacement. We refer the reviewer to their third point, about whether stable patterns of brain organization were artefactual. 

The introduction is overly long and includes numerous examples that can distract readers unfamiliar with the topic from the main research questions. 

We have removed the following from the Introduction, reducing it to just under 900 words:

“At a molecular level, early developmental patterning of the cortex arises through interacting gradients of morphogens and transcription factors (see Cadwell et al., 2019). The resultant areal and progenitor specialisation produces a diverse pool of neurones, glia, and astrocytes (Hawrylycz et al., 2015). Across childhood, an initial burst in neuronal proliferation is met with later protracted synaptic pruning (Bethlehem et al., 2022), the dynamics of which are governed by an interplay between experience-dependent synaptic plasticity and genomic control (Gottlieb, 2007)”.

“The trends described above reflect group-level developmental trends, but how do we capture these broad anatomical and functional organisational principles at the level of an individual?”

We’ve also trimmed the second Introduction paragraph so that it includes fewer examples, such as removal of the wiring-cost optimisation that underlies structural brain development, as well as removing specific instances of network segregation and integration that occur throughout childhood.

Author response:

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

Reviewer #1 (Public Review): 

Strengths: 

The work uses a simple and straightforward approach to address the question at hand: is dynein a processive motor in cells? Using a combination of TIRF and spinning disc confocal microscopy, the authors provide a clear and unambiguous answer to this question. 

Thank you for the recognition of the strength of our work

Weaknesses: 

My only significant concern (which is quite minor) is that the authors focus their analysis on dynein movement in cells treated with docetaxol, which could potentially affect the observed behavior. However, this is likely necessary, as without it, motility would not have been observed due to the 'messiness' of dynein localization in a typical cell (e.g., plus end-tracking in addition to cargo transport).

You are exactly correct that this treatment was required to provided us a clear view of motile dynein and p50 puncta. One concern about the treatment that we had noted in our original submission was that the docetaxel derivative SiR tubulin could increase microtubule detyrosination, which has been implicated in affecting the initiation of dynein-dynactin motility but not motility rates (doi: 10.15252/embj.201593071). In response to a comment from reviewer 2 we investigated whether there was a significant increase in alpha-tubulin detyrosination in our treatment conditions and found that there was not. We have removed the discussion of this possibility from the revised version. Please also see response to comments raised by reviewer 2. 

Reviewer 1 (Recommendations for the authors):

Major points: 

(1) The authors measured kinesin-1-GFP intensities in a different cell line (drosophila S2 cells) than what was used for the DHC and p50 measurements (HeLa cells). It is unclear if this provides a fair comparison given the cells provide different environments for the GFP. Although the differences may in fact be trivial, without somehow showing this is indeed a fair comparison, it should at least be noted as a caveat when interpreting relative intensity differences. Alternatively, the authors could compare DHC and p50 intensities to those measured from HeLa cells treated with taxol. 

Thank you for this suggestion. We conducted new rounds of imaging with the DHCEGFP and p50-EGFP clones in conjunction with HeLa cells transiently expressing the human kinesin-1-EGFP and now present the datasets from the new experiments. Importantly, our new data was entirely consistent with the prior analyses as there was not a significant difference between the kinesin-1-EGFP dimer intensities and the DHC-EGFP puncta intensities and there was a statistically significant difference in the intensity of p50 puncta, which were approximately half the intensity of the kinesin-1 and DHC. We have moved the old data comparing the intensities in S2 cells expressing kinesin-1-EGFP to Figure 3 - figure supplement 2 A-D and the new HeLa cell data is now shown in Figure 3 D-G.

(2) Given the low number of observations (41-100 puncta), I think a scatter plot showing all data points would offer readers a more transparent means of viewing the single-molecule data presented in Figures 3A, B, C, and G. I also didn't see 'n' values for plots shown in Figure 3. 

The box and whisker plots have now been replaced with scatter plots showing all data points. The accompanying ‘n’ values have been included in the figure 3 legend as well as the histograms in figures 1 and 2 that are represented in the comparative scatter plots.  

(3) Given the authors have produced a body of work that challenges conclusions from another pre-print (Tirumala et al., 2022 bioRxiv) - specifically, that dynein is not processive in cells - I think it would be useful to include a short discussion about how their work challenges theirs. For example, one significant difference between the two experimental systems that may account for the different observations could simply be that the authors of the Tirumala study used a mouse DHC (in HeLa cells), which may not have the ability to assemble into active and processive dynein-dynactin-adaptor complexes. 

Thank you for pointing this out! At the time we submitted our manuscript we were conflicted about citing a pre-print that had not been peer reviewed simply to point out the discrepancy. If we had done so at that time we would have proposed the exact potential technical issue that you have proposed here. However, at the time we felt it would be better for these issues to be addressed through the review process. Needless to say, we agree with your interpretation and now that the work is published (Tirumala et al. JCB, 2024) it is entirely appropriate to add a discussion on Tirumala et al. where contradictory observations were reported. 

The following statement has been added to the manuscript: 

“In contrast, a separate study (Tirumala et al., 2024) reported that dynein is not highly processive, typically exhibiting runs of very short duration (~0.6 s) in HeLa cells. A notable technical difference that may account for this discrepancy is that our study visualizes endogenously tagged human DHC, whereas Tirumala et al. characterized over-expressed mouse DHC in HeLa cells. Over-expression of the DHC may result in an imbalance of the subunits that comprise the active motor complex, leading to inactive, or less active complexes. Similarly, mouse DHC may not have the ability to efficiently assemble into active and processive dynein-dynactin-adaptor complexes to the same extent as human DHC.”

Minor points: 

(1) "Specifically, the adaptor BICD2 recruited a single dynein to dynactin while BICDR1 and HOOK3 supported assembly of a "double dynein" complex." It would be more accurate to say that dynein-dynactin complexes assembled with Bicd2 "tend to favor single dynein, and the Bicdr1 and Hook3 tend to favor two dyneins" since even Bicd2 can support assembly of 2 dynein-1 dynactin complexes (see Urnavicius et al, Nature 2018). 

Thank you, the manuscript has been edited to reflect this point. 

(2) "Human HeLa cells were engineered using CRISPR/Cas9 to insert a cassette encoding FKBP and EGFP tags in the frame at the 3' end of the dynein heavy chain (DYNC1H1) gene (SF1)." It is unclear to what "SF1" is referring. 

SF1 is supplementary figure 1, which we have now clarified as being Figure 1 – figure supplement 1A.

(3) "The SiR-Tubulin-treated cells were subjected to two-color TIRFM to determine if the DHC puncta exhibited motility and; indeed, puncta were observed streaming along MTs..." This sentence is strangely punctuated (the ";" is likely a typo?). 

Thank you for pointing this out, the typo has been corrected and the sentence now reads:

“The SiR-Tubulin-treated cells were subjected to two-color TIRFM and DHC-EGFP puncta were clearly observed streaming on Sir-Tubulin labeled MTs, which was especially evident on MTs that were pinned between the nucleus and the plasma membrane (Video 3)”

(4) I am unfamiliar with the "MK" acronym shown above the molecular weight ladders in Figure 3H and I. Did the authors mean to use "MW" for molecular weight? 

We intended this to mean MW and the typo has been corrected.

(5) "This suggests that the cargos, which we presume motile dynein-dynactin puncta are bound to, any kinesins..." This sentence is confusing as written. Did the authors mean "and kinesins"? 

Agreed. We have changed this sentence to now read: 

“The velocity and low switching frequency of motile puncta suggest that any kinesin motors associated with cargos being transported by the dynein-dynactin visualized here are inactive and/or cannot effectively bind the MT lattice during dynein-dynactin-mediated transport in interphase HeLa cells.”

Reviewer 2 (Recommendations for the authors):

(1) I am confused as to why the authors introduced an FKBP tag to the DHC and no explanation is given. Is it possible this tag induces artificial dimerization of the DHC? 

FKBP was tagged to DHC for potential knock sideways experiments. Since the current cell line does not express the FKBP counterpart FRB, having FKBP alone in the cell line would not lead to artificial dimerization of DHC.

(2) The authors use a high concentration of SiR-tubulin (1uM) before washing it out. However, they observe strong effects on MT dynamics. The manufacturer states that concentrations below 100nM don't affect MT dynamics, so I am wondering why the authors are using such a high amount that leads to cellular phenotypes. 

We would like to note that in our hands even 100 nM SiR-tubulin impacted MT dynamics if it was incubated for enough time to get a bright signal for imaging, which makes sense since drugs like docetaxel and taxol become enriched in cells over time. Thus, it was a trade-off between the extent/brightness of labeling and the effects on MT dynamics. We opted for shorter incubation with a higher concentration of Sir-Tubulin to achieve rapid MT labeling and efficient suppression of plus-end MT polymerization. This approach proved useful for our needs since the loss of the tip-tacking pool of DHC provided a clearer view of the motile population of MT-associated DHC.

(3) The individual channels should be labeled in the supplemental movies. 

They have now been labelled.

(4) I would like to see example images and kymographs of the GFP-Kinesin-1 control used for fluorescent intensity analysis. Further, the authors use the mean of the intensity distribution, but I wonder why they don't fit the distribution to a Gaussian instead, as that seems more common in the field to me. Do the data fit well to a Gaussian distribution? 

Example images and kymographs of the kinesin-1-EGFP control HeLa cells used for the updated fluorescent intensity analysis have been now added to the manuscript in Figure 3 - figure supplement 1. The kinesin-1-EGFP transiently expressed in HeLa cells exhibited a slower mean velocity and run length than the endogenously tagged HeLa dynein-dynactin. Regarding the distribution, we applied 6 normality tests to the new datasets acquired with DHC and p50 in comparison to human kinesin-EGFP in HeLa cells. While we are confident concluding that the data for p50 was normally distributed (p > 0.05 in 6/6), it was more difficult to reach conclusions about the normality of the datasets for kinesin-1 (p > 0.05 in 4/6) and DHC (p > 0.5 in 1/6). We have decided to report the data as scatter plots (per the suggestion in major point 1 by reviewer 1) in the new Figure 3G since it could be misleading to fit a non-normal distribution with a single Gaussian. We note that the likely non-normal distribution of the DHC data (since it “passed” only 1/6 normality tests) could reflect the presence of other populations (e.g. 1 DHC-EGFP in a motile puncta), but we could also not confidently conclude this since attempting to fit the data with a double Gaussian did not pass statistical muster. Indeed, as stated in the text, on lines 197-198 we do not exclude that the range of DHC intensities measured here may include sub-populations of complexes containing a single dynein dimer with one DHC-EGFP molecule.   

Ultimately, we feel the safest conclusion is that there was not a statically significant difference between the DHC and kinesin-1 dimers (p = 0.32) but there was a statistically significant difference between both the DHC and kinesin-1 dimers compared to the p50 (p values < 0.001), which was ~50% the intensity of DHC and kinesin-1. Altogether this leads us to the fairly conservative conclusion that DHC puncta contain at least one dimer while the p50 puncta likely contain a single p50-EGFP molecule. 

(5) The authors suggest the microtubules in the cells treated with SiR-tubulin may be more detyrosinated due to the treatment. Why don't they measure this using well-characterized antibodies that distinguish tyrosinated/detyrosinated microtubules in cells treated or not with SiR-tubulin? 

At your suggestion, we carried out the experiment and found that under our labeling conditions there was not a notable difference in microtubule detyrosination between DMSO- and SiR-Tubulin-treated cells. Thus, we have removed this caveat from the revised manuscript.

(6) "While we were unable to assess the relative expression levels of tagged versus untagged DHC for technical reasons." Please describe the technical reasons for the inability to measure DHC expression levels for the reader.

We made several attempts to quantify the relative amounts of untagged and tagged protein by Western blotting. The high molecular weight of DHC (~500kDa) makes it difficult to resolve it on a conventional mini gel. We attempted running a gradient mini gel (4%-15%), and doing a western blot; however, we were still unable to detect DHC. To troubleshoot, the experiments were repeated with different dilutions of a commercially available antibody and varying concentrations of cell lysate; however, we were unable to obtain a satisfactory result. 

We hold the view that even if it had it worked it would have been difficult to detect a relatively small difference between the untagged (MW = 500kDa) and tagged DHC (MW = 527kDa) by western blot. We have added language to this effect in the revised manuscript. 

Reviewer #3 (Public Review):

(1). CRISPR-edited HeLa clones: 

(i) The authors indicate that both the DHC-EGFP and p50-EGFP lines are heterozygous and that the level of DHC-EGFP was not measured due to technical difficulties. However, quantification of the relative amounts of untagged and tagged DHC needs to be performed - either using Western blot, immunofluorescence or qPCR comparing the parent cell line and the cell lines used in this work. 

See response to reviewer 2 above. 

(ii) The localization of DHC predominantly at the plus tips (Fig. 1A) is at odds with other work where endogenous or close-to-endogenous levels of DHC were visualized in HeLa cells and other non-polarized cells like HEK293, A-431 and U-251MG (e.g.: OpenCell (https://opencell.czbiohub.org/target/CID001880), Human Protein Atlas  ), https://www.biorxiv.org/content/10.1101/2021.04.05.438428v3). The authors should perform immunofluorescence of DHC in the parental cells and DHC-EGFP cells to confirm there are no expression artifacts in the latter. Additionally, a comparison of the colocalization of DHC with EB1 in the parental and DHC-EGFP and p50-EGFP lines would be good to confirm MT plus-tip localisation of DHC in both lines. 

The microtubule (MT) plus-tip localization of DHC was already observed in the 1990s, as evidenced by publications such as (PMID:10212138) and (PMID:12119357), which were further confirmed by Kobayashi and Murayama  in 2009 (PMID:19915671). We hold the view that further investigation into this localization is not worthwhile since the tip-tracking behavior of DHC-dynactin has been long-established in the field.

(iii) It would also be useful to see entire fields of view of cells expressing DHC-EGFP and p50EGFP (e.g. in Spinning Disk microscopy) to understand if there is heterogeneity in expression. Similarly, it would be useful to report the relative levels of expression of EGFP (by measuring the total intensity of EGFP fluorescence per cell) in those cells employed for the analysis in the manuscript. 

Representative images of fields have been added as Figure 1 - figure supplement 1B and Figure 2 – figure supplement 1 in the revised manuscript. We did not see drastic cell-tocell variation of expression within the clonal cell lines.

(iv) Given that the authors suspect there is differential gene regulation in their CRISPR-edited lines, it cannot be concluded that the DHC-EGFP and p50-EGFP punctae tracked are functional and not piggybacking on untagged proteins. The authors could use the FKBP part of the FKBPEGFP tag to perform knock-sideways of the DHC and p50 to the plasma membrane and confirm abrogation of dynein activity by visualizing known dynein targets such as the Golgi (Golgi should disperse following recruitment of EGFP-tagged DHC-EGFP or p50-EGFP to the PM), or EGF (movement towards the cell center should cease). 

Despite trying different concentrations and extensive troubleshooting, we were not able to replicate the reported observations of Ciliobrevin D or Dynarrestin during mitosis. We would like to emphasize that the velocity (1.2 μm/s) of dynein-dynactin complexes that we measured in HeLa cells was comparable to those measured in iNeurons by Fellows et al. (PMID: 38407313) and for unopposed dynein under in vitro conditions. 

(2) TIFRM and analysis: 

(i) What was the rationale for using TIRFM given its limitation of visualization at/near the plasma membrane? Are the authors confident they are in TIRF mode and not HILO, which would fit with the representative images shown in the manuscript? 

To avoid overcrowding, it was important to image the MT tracks that that were pinned between the nucleus and the plasma membrane. It is unclear to us why the reviewer feels that true TIRFM could not be used to visualize the movement of dynein-dynactin on this population of MTs since the plasma membrane is ~ 3-5 nm and a MT is ~25-27 nm all of which would fall well within the 100-200 nm excitable range of the evanescent wave produced by TIRF. While we feel TIRF can effectively visualize dynein-dynactin motility in cells, we have mentioned the possibility that some imaging may be HILO microscopy in the materials and methods.

(ii) At what depth are the authors imaging DHC-EGFP and p50-EGFP? 

The imaging depth of traditional TIRFM is limited to around 100-200 nm. In adherent interphase HeLa cells the nucleus is in very close proximity (nanometer not micron scale) to the plasma membrane with some cytoskeletal filaments (actin) and microtubules positioned between the plasma membrane and the nuclear membrane. The fact that we were often visualizing MTs positioned between the nucleus and the membrane makes us confident that we were imaging at a depth (100 - 200nm) consistent with TIRFM. 

(iii) The authors rely on manual inspection of tracks before analyzing them in kymographs - this is not rigorous and is prone to bias. They should instead track the molecules using single particle tracking tools (eg. TrackMate/uTrack), and use these traces to then quantify the displacement, velocity, and run-time. 

Although automated single particle tracking tools offer several benefits, including reduced human effort, and scalability for large datasets, they often rely on specialized training datasets and do not generalize well to every dataset. The authors contend that under complex cellular environments human intervention is often necessary to achieve a reliable dataset. Considering the nature of our data we felt it was necessary to manually process the time-lapses. 

(iv) It is unclear how the tracks that were eventually used in the quantification were chosen. Are they representative of the kind of movements seen? Kymographs of dynein movement along an entire MT/cell needs to be shown and all punctae that appear on MTs need to be tracked, and their movement quantified. 

Considering the densely populated environment of a cell, it will be nearly impossible to quantity all the datasets. We selected tracks for quantification, focusing on areas where MTs were pinned between the nucleus and plasma membrane where we could track the movement of a single dynein molecule and where the surroundings were relatively less crowded. 

(v) What is the directionality of the moving punctae? 

In our experience, cells rarely organized their MTs in the textbook radial MT array meaning that one could not confidently conclude that “inward” movements were minus-end directed. Microtubule polarity was also not able to be determined for the MTs positioned between the plasma membrane and the nucleus on which many of the puncta we quantified were moving. It was clear that motile puncta moving on the same MT moved in the same direction with the exception of rare and brief directional switching events. What was more common than directional switching on the same MT were motile puncta exhibiting changes in direction at sharp (sometimes perpendicular) angles indicative of MT track switching, which is a well-characterized behavior of dynein-dynactin (See DOI: 10.1529/biophysj.107.120014).

(vi) Since all the quantification was performed on SiR tubulin-treated cells, it is unclear if the behavior of dynein observed here reflects the behavior of dynein in untreated cells. Analysis of untreated cells is required. 

It was important to quantify SiR tubulin-treated cells because SiR-Tubulin is a docetaxel derivative, and its addition suppressed plus-end MT polymerization resulting in a significant reduction in the DHC tip-tracking population and a clearer view of the motile population of MT-associated DHC puncta. Otherwise, it was challenging to reliably identify motile puncta given the abundance of DHC tip-tracking populations in untreated cells.  

(3) Estimation of stoichiometry of DHC and p50 

Given that the punctae of DHC-EGFP and p50 seemingly bleach on MT before the end of the movie, the authors should use photobleaching to estimate the number of molecules in their punctae, either by simple counting the number of bleaching steps or by measuring single-step sizes and estimating the number of molecules from the intensity of punctae in the first frame. 

Comparing the fluorescence intensity of a known molecule (in our case a kinesin-1EGFP dimer) to calculate the numbers of an unknown protein molecule (in our case Dynein or p50) is a widely accepted technique in the field. For example, refer to PMID: 29899040. To accurately estimate the stoichiometry of DHC and p50 and address the concerns raised by other reviewers, we expressed the human kinesin-EGFP in HeLa cells and analyzed the datasets from new experiments. We did not observe any significant differences between our old and new datasets.

(4) Discussion of prior literature 

Recent work visualizing the behavior of dyneins in HeLa cells (DOI:  10.1101/2021.04.05.438428), which shows results that do not align with observations in this manuscript, has not been discussed. These contradictory findings need to be discussed, and a more objective assessment of the literature in general needs to be undertaken.

Author response:

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

Reviewer #1 (Public review):

Summary:

This study focuses on the bacterial metabolite TMA, generated from dietary choline. These authors and others have previously generated foundational knowledge about the TMA metabolite TMAO, and its role in metabolic disease. This study extends those findings to test whether TMAO's precursor, TMA, and its receptor TAAR5 are also involved and necessary for some of these metabolic phenotypes. They find that mice lacking the host TMA receptor (Taar5-/-) have altered circadian rhythms in gene expression, metabolic hormones, gut microbiome composition, and olfactory and innate behavior. In parallel, mice lacking bacterial TMA production or host TMA oxidation have altered circadian rhythms.

Strengths:

These authors use state-of-the-art bacterial and murine genetics to dissect the roles of TMA, TMAO, and their receptor in various metabolic outcomes (primarily measuring plasma and tissue cytokine/gene expression). They also follow a unique and unexpected behavioral/olfactory phenotype. Statistics are impeccable.

Weaknesses:

Enthusiasm for the manuscript is dampened by some ambiguous writing and the presentation of ideas in the introduction, both of which could easily be improved upon revision.

We apologize for the abbreviated and ambiguous writing style in our original submission. Given Reviewer 2 also suggested reorganizing and rewriting certain parts, we have spent time to remove ambiguity by adding additional points of clarification and adding more historical context to justify studying TMA-TAAR5 signaling in regulating host circadian rhythms. We have also reorganized the presentation of data aligned with this.

Reviewer #2 (Public review):

Summary:

In the manuscript by Mahen et al., entitled "Gut Microbe-Derived Trimethylamine Shapes Circadian Rhythms Through the Host Receptor TAAR5," the authors investigate the interplay between a host G protein-coupled receptor (TAAR5), the gut microbiota-derived metabolite trimethylamine (TMA), and the host circadian system. Using a combination of genetically engineered mouse and bacterial models, the study demonstrates a link between microbial signaling and circadian regulation, particularly through effects observed in the olfactory system. Overall, this manuscript presents a novel and valuable contribution to our understanding of hostmicrobe interactions and circadian biology. However, several sections would benefit from improved clarity, organization, and mechanistic depth to fully support the authors' conclusions.

Strengths:

(1) The manuscript addresses an important and timely topic in host-microbe communication and circadian biology.

(2) The studies employ multiple complementary models, e.g., Taar5 knockout mice, microbial mutants, which enhance the depth of the investigation.

(3) The integration of behavioral, hormonal, microbial, and transcript-level data provides a multifaceted view of the observed phenotype.

(4) The identification of olfactory-linked circadian changes in the context of gut microbes adds a novel perspective to the field.

Weaknesses:

While the manuscript presents compelling data, several weaknesses limit the clarity and strength of the conclusions.

(1) The presentation of hormonal, cytokine, behavioral, and microbiome data would benefit from clearer organization, more detailed descriptions, and functional grouping to aid interpretation.

We appreciate this comment and have reorganized the data to improve functional grouping and readability. We have also added additional detail to descriptions of the data in the revised figure legends and results.

(2) Some transitions-particularly from behavioral to microbiome data-are abrupt and would benefit from better contextual framing.

We agree with this comment, and have added additional language to provide smoother transitions. This in many cases brings in historical context of why we focused on both behavioral and microbiome alterations in this body of work.

(3) The microbial rhythmicity analyses lack detail on methods and visualization, and the sequencing metadata (e.g., sample type, sex, method) are not clearly stated.

We apologize for this, and have now added more detail in our methods, figures, and figure legends to ensure the reader can easily understand sample type, sex, and the methods used. 

(4) Several figures are difficult to interpret due to dense layouts or vague legends, and key metabolites and gene expression comparisons are either underexplained or not consistently assessed across models.

Aligned with the last comment we now added more detail in our methods, figures, and figure legends to provide clear information. We have now provided additional data showing the same key metabolites, hormones, and gene expression alterations in each model if the same endpoints were measured.

(5) Finally, while the authors suggest a causal role for TAAR5 and its ligand in circadian regulation, the current data remain correlative; mechanistic experiments or stronger disclaimers are needed to support these claims.

We agree with this comment, and as a result have removed any language causally linking TMA and TAAR5 together in circadian regulation. Instead, we only state finding in each model and refrain from overinterpreting.

Reviewer #3 (Public review):

Summary:

Deletion of the TMA-sensor TAAR5 results in circadian alterations in gene expression, particularly in the olfactory bulb, plasma hormones, and neurobehaviors.

Strengths:

Genetic background was rigorously controlled.

Comprehensive characterization.

Weaknesses:

The weaknesses identified by this reviewer are minor.

Overall, the studies are very nicely done. However, despite careful experimentation, I note that even the controls vary considerably in their gene expression, etc, across time (eg, compare control graphs for Cry 1 in IB, 4B). It makes me wonder how inherently noisy these measurements are. While I think that the overall point that the Taar5 KO shows circadian changes is robust, future studies to dissect which changes are reproducible over the noise would be helpful.

We thank the reviewer for this insightful comment. We completely agree that there are clear differences in the circadian data in experiments from Taar5^-/- mice and those from gnotobiotic mice where we have genetically deleted CutC. Although the data from Taar5^-/- mice show nice robust circadian rhythms, the data from mice where microbial CutC is altered have inherently more “noise”. We attribute some of this to the fact that the Taar5^-/- mouse experiment have a fully intact and diverse gut microbiome . Whereas, the gnotobiotic study with CutC manipulation includes only a 6 member microbiome community that does not represent the normal microbiome diversity in the gut. This defined synthetic community was used as a rigorous reductionist approach, but likely affected the normal interactions between a complex intact gut microbiome and host circadian rhythms. We have added some additional discussion to indicate this in the limitations section of the manuscript.

Impact:

These data add to the growing literature pointing to a role for the TMA/TMAO pathway in olfaction and neurobehavioral.

Reviewer #1 (Recommendations for the authors):

I suggest a revision of the writing and organization. The potential impact of the study after reading the introduction is unclear. One example, in the intro, " TMAO levels are associated with many human diseases including diverse forms of CVD5-12, obesity13,14, type 2 diabetes15,16, chronic kidney disease (CKD)17,18, neurodegenerative conditions including Parkinson's and Alzheimer's disease19,20, and several cancers21,22" It would be helpful to explain how the previous literature has distinguished that the driver of these phenotypes is TMA/TMAO and not increased choline intake. Basically, for a TMA/O novice reader, a more detailed intro would be helpful.

We appreciate this insightful comment and have now provided a more expansive historical context for the reader regarding the effects of choline consumption (which impacts many things, including choline, acetylcholine, phosphatidylcholine, TMA, TMAO, etc) versus the primary effects of TMA and TMAO.

There were also many uses of vague language (regulation/impact/etc). Directionality would be super helpful.

We thank the reviewer for this recommendation and have improved language as suggested to show directionality of our findings. The terms regulation, impact, shape etc. are used only when we describe multiple variable changing at the same time over the time course of a 24-hour circadian period (some increased and some decreased).

Reviewer #2 (Recommendations for the authors):

In the manuscript by Mahen et al., entitled "Gut Microbe-Derived Trimethylamine Shapes Circadian Rhythms Through the Host Receptor TAAR5," the authors investigate the interplay between a host G protein-coupled receptor (TAAR5), the gut microbiota-derived metabolite trimethylamine (TMA), and the host circadian system. Using a combination of genetically engineered mouse and bacterial models, the study demonstrates a link between microbial signaling and circadian regulation, particularly through effects observed in the olfactory system. Overall, this manuscript presents a novel and valuable contribution to our understanding of hostmicrobe interactions and circadian biology. However, several sections would benefit from improved clarity, organization, and mechanistic depth to fully support the authors' conclusions. Below are specific major and minor suggestions intended to enhance the presentation and interpretation of the data.

Major suggestions:

(1) Consider adding a schematic/model figure as Panel A early in the manuscript to help readers understand the experimental conditions and major comparisons being made.

We thank the reviewer for this recommendation and have added a graphical abstract figure to help the reader understand the major comparisons being made. 

(2) Could the authors present body weight and food intake characteristics in Taar5 KO vs. WT animals?

We have added body weight data as requested in Figure 1, Figure supplement 1. Although we have not stressed these mice with a high fat diet for these behavioral studies, under chow-fed conditions studied here we did not find any significant differences in body weight. Given no difference in body weight, we did not collect data on food consumption and have mentioned this as a limitation in the discussion.  

(3) Several figures, especially Figures 3 and 4, and Supplemental Figures, would benefit from more structured organization and expanded legends. Grouping related data into thematic panels (e.g., satiety vs. appetite hormones, behavioral domains) may help improve readability.

We appreciate the reviewer’s thoughtful comments and agree that reorganization would improve clarity. We have reorganized figures to improve clarity and have expanded the figure legends to provide more detail on experimental methods. 

(4) Clarify and expand the description of hormonal and cytokine changes. For instance, the phrase "altered rhythmic levels" is vague - do the authors mean dampened, phase-shifted, enhanced, etc., relative to WT controls?

Given a similar suggestion was made by Reviewer 1, we have provided more precise language focused on directionality and which specific endpoints we are referring to. For anything looking at circadian rhythms, the revised manuscript includes specific indications when we are discussing mesor, amplitude, and acrophase alterations. The terms regulation, impact, shape etc. are used only when we describe multiple complex variables changing at the same time over the time course of a 24-hour circadian period (some increased and some decreased).

(5) Consider grouping hormones and cytokines functionally (e.g., satiety vs. appetite-stimulating, pro- vs. antiinflammatory) to better interpret how these changes relate to the KO phenotype.

We thank the reviewer for this recommendation, and have re-organized figure panels to reflect this.

(6) Please provide a more detailed description of the behavioral results, particularly those in Supplemental Figure 2.

We have both expanded the methods description in the revised figure legends, but have also added a more detailed description of the behavioral results.

(7) As with hormonal data, behavioral outcomes would be easier to follow if organized thematically (e.g., locomotor activity, anxiety-like behavior, circadian-related behavior), especially for readers less familiar with behavioral assays.

We appreciate this reviewer’s comment and agree that we can better group our data to show how each test is associated with the type of behavior it assesses. As a result we have reorganized the behavioral data into broad categories such as olfactory-related, innate, cognitive, depressive/anxiety-like, or social behaviors. We have also new data in each of these behavioral categories to provide a more comprehensive understanding of behavioral alterations seen in Taar5^-/- mice.

(8) The following statement needs clarification: "Also, it is important to note that many behavioral phenotypes examined, including tests not shown, were unaltered in Taar5-/- mice (Figures S2G, S2H, and S2I)." Consider rephrasing to explicitly state the intended message: are the authors emphasizing a lack of behavioral phenotype, or highlighting specific unaltered aspects?

We apologize for this confusing statement, and have changed the verbiage to improve readability. To expand the comprehensive nature of this study, we also now include the tests that were “not shown” in the original submission to provide a more comprehensive understanding of behavioral alterations seen in Taar5^-/- mice. These new data are included as 6 different figure supplements to main Figure 2.

(9) The transition from behavior to microbiome data feels abrupt. Can the authors better explain whether the behavioral changes are thought to result from gut microbial function, independent of TMA-Taar5 signaling?

We apologize for the poor transitions in our writing style. We have spent time to explain the previous findings linking the TMA pathway to circadian reorganization of the gut microbiome (mostly coming from our original paper Schugar R, et al. 2022, eLife) and how this correlates with behavioral phenotypes. Although at this point it is difficult to know whether the microbiome changes are driving behavioral changes, or vice versa it could be central TAAR5 signaling is altering oscillations in gut microbiome, we present our findings here as a framework for follow up studies to more precisely get at these questions. It is important to note that our experiment using defined community gnotobiotic mice with or without the capacity to produce TMA (i.e. CutC-null community) shows that clearly microbial TMA production can impact host circadian rhythms in the olfactory bulb. Additional experiments beyond the scope of this work will be required to test which phenotypes originate from TMA-TAAR5 signaling versus more broad effects of the restructured gut microbiome.

(10) For Figure 3A, please expand the microbiome results with more granularity:

(a) Indicate in the Results section whether the sequencing method was 16S amplicon or metagenomic.

Sequencing was done using 16S rRNA amplicon sequencing using methods published by our group (PMID: 36417437, PMID: 35448550).

(b) State whether samples were from males, females, or a mix. 

We have indicated that all mice from Figure 1 were male mice in the revised figure legend.

(c) Clarify whether beta diversity is based on phylogenetic or non-phylogenetic metrics. Consider using both  types if not already done.

Beta diversity was analyzed using the Bray-Curtis dissimilarity index as the metric. Details have been included in the methods section.

(d) Make lines partially transparent in the Beta-diversity plot so that individual points are visible.

We have now updated the Beta-diversity plot with individual points visualized.

(e) Clarify what percentage of variation in the Beta-diversity plot is explained by CCA1, and whether this low percentage suggests minimal community-level differences.

We have updated the Beta-diversity plot to include the R² and p-values associated with these data.

(f) Confirm if the y-axis on the Beta-diversity plot should be labeled CCA2 rather than "CCAA 1".

We appreciate this comments, given it identified a typographical error in the plot. The revised figure now include the proper label of CCA2 instead of CCAA 1.

(11) For Figure 3B:

(a) Provide a description of the taxonomy plot in the results.

We have added a description of the taxonomy plot in the revised results section.

(b) Add phylum-level labels and enlarge the legend to improve the readability of genus-level data.

We agree this is a good suggestion so have enlarged the legend for the genus-level data and have also added phylum-level plots as well in the revised manuscript in Figure 3, figure supplement 1.

(12) Rhythmicity of the microbiome is central to the manuscript. The current approach of comparing relative abundance at discrete time points is limiting.

We thank the reviewer for this comment. We agree with this statement that discrete timepoint are not enough to describe circadian rhythmicity. In addition to comparing genotypes at discrete time points, we also used a rigorous cosinor analysis to plot the data over a 24-hour time period, and those differences are shown in the figure itself as well as Table 1. 

(a) Please describe how rhythmicity was determined, e.g., what data or statistical method supports the statement: "Taar5-/- mice showed loss of the normal rhythmicity for Dubosiella and Odoribacter genera yet gained in amplitude of rhythmicity for Bacteroides genera (Figure 3 and S3)."

We appreciate this reviewer comment. Rhythmicity was determined using a cosinor analysis by use of an R program. Cosinor analysis is a statistical method used to model and analyze rhythmic patterns in time-series data, typically assuming a sinusoidal (cosine) shape. It estimates key parameters like mesor (mean level), amplitude (height of oscillation), and acrophase (timing of the peak), making it especially useful in fields like chronobiology and circadian rhythm research. We have used this in previous research to describe circadian rhythms. We do plan to improve language considering directionality of these circadian changes. 

(b) Supplemental Figure S3 needs reorganization to highlight key findings. It's not currently clear how taxa are arranged or what trends are being shown.

The data in Figure S3 show the entire 24-hour time course of the cecal taxa that were significantly altered for at least one time point between Taar5^+/+ and Taar5^-/- mice. Given we showed time pointspecific alterations in the Main Figure 3, we thought these more expansive plots would be important to show to depict how the circadian rhythms were altered.

(c) Supplemental Table 1, which includes 16S features, should be referenced and discussed in the microbiome section.

We have now referenced and discussed Supplemental Table 1 which includes all cosinor statistics for microbiome and other data presented in circadian time point studies.

(13) Did the authors quantify the 16S rRNA gene via RT-PCR to determine if this was similar between KO and WT over the 24-hour period?

We did not quantify 16S rRNA gene via RT-PCR, but do not think adding this will change our overall interpretations.

(14) Reorganize Figure 4 to align with the order of results discussed-starting with TMA and TMAO, followed by related metabolites like choline, L-carnitine, and gamma-butyrobetaine.

We thank the reviewer for this comment. We have chosen this organization because it is ordered from substrates (choline, L-carnitine, and betaine) to the microbe-associated products (TMA then TMAO). We will improve the writing associated with this figure to clearly explain this organization.

(a) Although the changes in the latter metabolites are more modest, they may still have physiological relevance. Could the authors comment on their significance?

We appreciate this reviewer comment and agree. We have expanded the results and discussion to address this.

(15) The authors note similarities in circadian gene expression between Taar5 KO mice and Clostridium sporogenes WT vs. ΔcutC mice, but the gene patterns are not consistent.

(a) Can the authors clarify what conclusions can reasonably be drawn from this comparison?

We hesitate to make definitive conclusions in the manuscript on why the gene patterns are not consistent, because it would be speculation. However, one major factor likely driving differences is the status of the diversity of the gut microbiome in the different studies. For instance, in the studies using Taar5^+/+ and Taar5^-/- mice there is a very diverse microbiome in these conventionally housed mice. In contrast, by design the experiment using Clostridium sporogenes WT vs. ΔcutC communities is a reductionist approach that allows us to genetically define TMA production. In these gnotobiotic mice, the simplified community has very limited diversity and this likely alters the host circadian rhythms in gene expression quite dramatically. Although it is impossible to directly compare the results between these experiments given the difference microbiome diversity, there are clearly alterations in host gene expression when we manipulate TMA production (i.e. ΔcutC community) or TMA sensing (i.e. Taar5^-/-). 

(16) Were circadian and metabolic genes (e.g., Arntl, Cry1, Per2, Pemt, Pdk4) also analyzed in brown adipose tissue of Taar5 KO mice, and how do these results compare to the Clostridium models?

We thank the reviewer for this comment. Unfortunately, we did not collect brown adipose tissue in our original Taar5 study. We plan on doing this in future follow up studies studying cold-induced thermogenesis that are beyond the scope of this manuscript. However, we have decided to include data from our two timepoint Taar5 study which looks at ZT2 (9am) and ZT14 (9pm). There are clear differences in circadian genes between these timepoints. 

(17) To allow a more direct comparison, please ensure the same cytokines (e.g., IL-1β, IL-2, TNF-α, IFN-γ, IL6, IL-33) are reported for both the Taar5 KO and microbial models.

We thank the reviewer for this comment and now include data from the same cytokines for each study.

(18) What was the defined microbial community used to colonize germ-free mice with C. sporogenes strains? Did this community exhibit oscillatory behavior?

To define TMA levels using a genetically-tractable model of a defined microbial community, we leveraged access to the community originally described by our collaborator Dr. Federico Rey (University of Wisconsin – Madison) (PMID: 25784704). We chose this community because it provide some functional metabolic diversity and is well known to allow for sufficient versus deficient TMA production. We are thankful for the reviewer comments about oscillatory behavior of this defined community, and to be responsive have performed sequencing to detect the species over time. These data are now included in the revised manuscript and show that there are clear differences in the oscillatory behavior of the defined community members. These data provide additional support that bacterial TMA production not only alters host circadian rhythms, but also the rhythmic behavior of gut bacteria themselves which has never been described before.

(19) Can the authors explain the rationale for measuring additional metabolites such as tryptophan, indole acetic acid, phenylacetic acid, and phenylacetylglycine? How are these linked to CutC gene function or Taar5 signaling?

We appreciate that this could be confusing, but have included other gut microbial metabolites to be as comprehensive as possible. This is important to include because we have found in other gnotobiotic studies where we have genetically altered metabolite production, if we alter one gut microbe-derived metabolite there can be unexpected alterations in other distinct classes of microbe-derived metabolites (PMID: 37352836). This is likely due to the fact that complex microbe-microbe and microbehost interactions work together to define systemic levels of circulating metabolites, influencing both the production and turnover of distinct and unrelated metabolites.

(20) The authors make several strong claims suggesting that loss of Taar5 or disruption of its ligand directly alters the circadian gene network. However, the current data are correlative. The authors should clarify that these findings demonstrate associations rather than direct causal effects, unless additional mechanistic evidence is provided. Approaches such as studies conducted in constant darkness, measurements of wheelrunning behavior, or analyses that control for potential confounding factors, e.g., inflammation or metabolic disruption, would help establish whether the observed changes in clock gene expression are primary or secondary effects. The authors are encouraged to either soften these causal claims or acknowledge this limitation explicitly in the discussion.

We thank the reviewer for this comment. We agree and have softened our language about direct effects of TMA via TAAR5 because we agree the data presented here are correlative only. 

Minor suggestions:

(1) Avoid repetitive phrases such as "it is important to note..." for improved flow. Rephrasing these instances will enhance readability.

We thank the reviewer for this suggestion and have deleted such repetitive phrases.  

(2) For Figure 2, remove interpretations above he graphs and use simple, descriptive panel labels, similar to those in Supplemental Figure 2.

We have removed these interpretations as suggested, but have retained descriptive panel labels to help the reader understand what type of data are being presented.

Reviewer #3 (Recommendations for the authors):

Minor:

In Figure 1D, UCP1 does not appear to be significantly changed.

We thank the reviewer for this comment and agree that UCP1 gene expression is not significantly altered . However, given the key role that UCP1 plays in white adipose tissue beiging, which is suppressed by the TMAO pathway, we think it is critical to show that this effect appears unaffected by perturbed TMA-TAAR5 signaling.

It would be helpful, in the discussion, to summarize any consistent changes across Taar5 KO, CutC deletion, and FMO3 deletion.

We have added this to the discussion, but as discussed above we hesitate to make strong interpretations about consistency between the models because the microbiome diversity is so different between the studies, and we did not measure all endpoints in both models.

For the Cosinor analysis, it may be helpful to remove the p-values that are >0.05 from the figures.

We have now removed any non-significant p-values that are associated with our figures. 

For Figure 2, Supplement 1E, what are the two bars for each genotype?

We appreciate the reviewer pointing this out and will further explain this test in the figure with labels and in the legend.

Author response:

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

Editors comments:

I would encourage you to submit a revised version that addresses the following two points:

[a] The point from Reviewer #1 about a possible major confounding factor. The following article might be germane here: Baas and Fennell, 2019: https://papers.ssrn.com/sol3/papers.cfm?abstract_id=3339568

I don’t believe that the point raised by reviewer 1 is a confounder, see my response below.

This article highlighted was in my reading list, but I did not cite it because I was confused by its methods.

The point from Reviewer #4 about the abstract. It is important that the abstract says something about how reviewers reacted to the original versions of articles in which they were cited (ie, the odds ratio = 0.84, etc result), before going on to discuss how they reacted to revised articles (ie, the odds ratio = 1.61, etc result). I would suggest doing this along the following lines - but please feel free to reword the passage "but this effect was not strong/conclusive":

When reviewers were cited in the original version of the article under review, they were less likely to approve the article compared with reviewers who were not cited, but this effect was not strong/conclusive (odds ratio = 0.84; adjusted 99.4% CI: 0.69-1.03). However, when reviewers were cited in the revised version of the article, they were more likely to approve compared with reviewers who were not cited (odds ratio = 1.61; adjusted 99.4% CI: 1.16-2.23).

I have changed the abstract to include the odds ratios for version 1 and have used the same wording as from the main text.

Reviewer #1 (Public review):

Summary:

The work used open peer reviews and followed them through a succession of reviews and author revisions. It assessed whether a reviewer had requested the author include additional citations and references to the reviewers' work. It then assessed whether the author had followed these suggestions and what the probability of acceptance was based on the authors decision. Reviewers who were cited were more likely to recommend the article for publication when compared with reviewers that were not cited. Reviewers who requested and received a citation were much likely to accept than reviewers that requested and did not receive a citation.

Strengths and weaknesses:

The work's strengths are the in-depth and thorough statistical analysis it contains and the very large dataset it uses. The methods are robust and reported in detail.

I am still concerned that there is a major confounding factor: if you ignore the reviewers requests for citations are you more likely to have ignored all their other suggestions too? This has now been mentioned briefly and slightly circuitously in the limitations section. I would still like this (I think) major limitation to be given more consideration and discussion, although I am happy that it cannot be addressed directly in the analysis.

This is likely to happen, but I do not think it’s a confounder. A confounder needs to be associated with both the outcome and the exposure of interest. If we consider forthright authors who are more likely to rebuff all suggestions, then they would receive just as many citation and self-citation requests as authors who were more compliant. The behaviour of forthright authors would likely only reduce the association seen in most authors which would be reflected in the odds ratios.

Reviewer #2 (Public review):

Summary:

This article examines reviewer coercion in the form of requesting citations to the reviewer's own work as a possible trade for acceptance and shows that, under certain conditions, this happens.

Strengths:

The methods are well done and the results support the conclusions that some reviewers "request" self-citations and may be making acceptance decisions based on whether an author fulfills that request.

Weakness:

I thank the author for addressing my comments about the original version.

Reviewer #3 (Public review):

Summary:

In this article, Barnett examines a pressing question regarding citing behavior of authors during the peer review process. In particular, the author studies the interaction between reviewers and authors, focusing on the odds of acceptance, and how this may be affected by whether or not the authors cited the reviewers' prior work, whether the reviewer requested such citations be added, and whether the authors complied/how that affected the reviewer decision-making.

Strengths:

The author uses a clever analytical design, examining four journals that use the same open peer review system, in which the identities of the authors and reviewers are both available and linkable to structured data. Categorical information about the approval is also available as structured data. This design allows a large scale investigation of this question.

Weaknesses:

My original concerns have been largely addressed. Much more detail is provided about the number of documents under consideration for each analysis, which clarifies a great deal.

Much of the observed reviewer behavior disappears or has much lower effect sizes depending on whether "Accept with Reservations" is considered an Accept or a Reject. This is acknowledged in the results text. Language has been toned down in the revised version.

The conditional analysis on the 441 reviews (lines 224-228) does support the revised interpretation as presented.

No additional concerns are noted.

Reviewer #4 (Public review):

Summary:

This work investigates whether a citation to a referee made by a paper is associated with a more positive evaluation by that referee for that paper. It provides evidence supporting this hypothesis. The work also investigates the role of self-citations by referees where the referee would ask authors to cite the referee's paper.

Strengths:

This is an important problem: referees for scientific papers must provide their impartial opinions rooted in core scientific principles. Any undue influence due to the role of citations breaks this requirement. This work studies the possible presence and extent of this.

The methods are solid and well done. The work uses a matched pair design which controls for article-level confounding and further investigates robustness to other potential confounds.

Weaknesses:

The authors have addressed most concerns in the initial review. The only remaining concern is the asymmetric reporting and highlighting of version 1 (null result) versus version 2 (rejecting null). For example the abstract says "We find that reviewers who were cited in the article under review were more likely to recommend approval, but only after the first version (odds ratio = 1.61; adjusted 99.4% CI: 1.16 to 2.23)" instead of a symmetric sentence "We find ... in version 1 and ... in version 2".

The latest version now includes the results for both versions.

Author response:

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

Reviewer #2 (Public review):

(1) Why would BPS not reduce RLS in WT cells? The authors could test whether OE of FIT2 reduces RLS in WT cells.  

Our data indicate that the iron regulon gets turned on naturally in old cells, presumably due to reduced iron sensing, limiting their lifespan. Although we haven’t tested it experimentally, BPS would also turn on the iron regulon presumably in wild type cells and therefore would have a redundant effect with the activation of the iron regulon that occurs naturally during normal aging. It may be interesting in the future to see if higher levels of BPS can shorten the lifespan of wildtype cells. Similarly, we would predict that overexpression of FIT2 may reduce the lifespan, as its deletion has been shown to extend RLS.  

(2) The authors should add a brief explanation for why the GDP1 promoter was chosen for Ssd1 OE.

We used the same promoter that was used to overexpress Ssd1 in all previous studies. This is now stated in the text along with the relevant citations. 

(3) On page 12, growth to saturation was described as glucose starvation. This is more accurately described as nutrient deprivation. Referring to it as glucose starvation is akin to CR, which growing to saturation is not. Ssd1 OE formed condensates upon saturation but not in CR. Why do the authors think Ssd1 OE did not form condensates upon CR?

Too mild a stress?

This is a fair comment, and we have now changed glucose starvation to nutrient deprivation, as it is more accurate. The effects of nutrient starvation are profound: the cell cycle stops, autophagy is induced, cells undergo the diauxic shift, metabolism changes. None of these changes occur during calorie restriction (0.05% glucose) such that it is not too surprising that Ssd1 does not form condensates during CR. We speculate that the stress is just too mild.   

(4) The authors conclude that the main mechanism for RLS extension in CR and Ssd1 OE is the inhibition of the iron regulon in aging cells. The data certainly supports this. However, this may be an overstatement as other mutations block CR, such as mutations that impair respiration. The authors do note that induction of the iron regulon in aging cells could be a response to impaired mitochondrial function. Thus, it seems that the main goal of CR and Ssd1 OE may be to restore mitochondrial function in aging cells, one way being inactivation of the iron regulon. A discussion of how other mutations impact CR would be of benefit.

While some labs have shown that respiration impacts CR, this is not the case in other studies. For example, an impactful paper by Kaeberlein et al., PLOS Genetics 2005 showed that CR does extend lifespan in respiratory deficient strains using many different strain backgrounds.

(5) The cell cycle regulation of Ssd1 OE condensates is very interesting. There does not appear to be literature linking Ssd1 with proteasome-dependent protein turnover. Many proteins involved in cell cycle regulation and genome stability are regulated through ubiquitination. It is not necessary to do anything here about it, but it would be interesting to address how Ssd1 condensates may be regulated with such precision.

we see no evidence of changes in Ssd1 protein intensity during the cell cycle. The difference therefore we speculate is at the post translational level rather than Ssd1 degradation and there are known cell cycle regulated phosphatase and kinase that regulates Ssd1 phosphorylation and condensation state whose timing of function match when the Ssd1 condensates appear and dissolve in the cell cycle. We have now discussed this and elude to it in the model. 

(6) While reading the draft, I kept asking myself what the relevance to human biology was. I was very impressed with the extensive literature review at the end of the discussion, going over how well conserved this strategy is in yeast with humans. I suggest referring to this earlier, perhaps even in the abstract. This would nail down how relevant this model is for understanding human longevity regulation.

Thank you, we have now mentioned in the abstract the relevance to human work. 

In conclusion, I enjoyed reading this manuscript, describing how Ssd1 OE and CR lead to RLS increases, using different mechanisms. However, since the 2 strategies appear to be using redundant mechanisms, I was surprised that synergism was not observed.

We thank the reviewer for their kind comment. We propose that Ssd1 overexpression impacts the levels of the iron regulon transcripts, which would be downstream of the point in the pathway that is affected by CR, i.e., nuclear localization of Aft1. The lack of synergy fits with this model, as Ssd1 overexpression cannot impact the iron regulon transcripts if they are not induced due to CR. We have now improved the model to make the impact of these different anti-aging interventions on activation of the iron regulon more clear.

Reviewer #3 (Public review):

My main concern is that the central reasoning of the paper-that Ssd1 overexpression and CR prevent the activation of the iron regulon-appears to be contradicted by previous findings, and the authors may actually be misrepresenting these studies, unless I am mistaken. In the manuscript, the authors state on two occasions:

"Intriguingly, transcripts that had altered abundance in CR vs control media and in SSD1 vs ssd1∆ yeast included the FIT1, FIT2, FIT3, and ARN1 genes of the iron regulon (8)"

"Ssd1 and CR both reduce the levels of mRNAs of genes within the iron regulon: FIT1, FIT2, FIT3 and ARN1 (8)"

However, reference (8) by Kaeberlein et al. actually says the opposite:

"Using RNA derived from three independent experiments, a total of 97 genes were observed to undergo a change in expression >1.5-fold in SSD1-V cells relative to ssd1d cells (supplemental Table 1 at http://www.genetics.org/supplemental/). Of these 97 genes, only 6 underwent similar transcriptional changes in calorically restricted cells (Table 2). This is only slightly greater than the number of genes expected to overlap between the SSD1-V and CR datasets by chance and is in contrast to the highly significant overlap in transcriptional changes observed between CR and HAP4 overexpression (Lin et al. 2002) or between CR and high external osmolarity (Kaeberlein et al. 2002). Intriguingly, of the 6 genes that show similar transcriptional changes in calorically restricted cells and SSD1-V cells, 4 are involved in ironsiderochrome transport: FIT1, FIT2, FIT3, and ARN1 (supplemental Table 1 at http://www.genetics.org/supplemental/)."

Although the phrasing might be ambiguous at first reading, this interpretation is confirmed upon reviewing Matt Kaeberlein's PhD thesis: https://dspace.mit.edu/handle/1721.1/8318 (page 264 and so on).

Moreover, consistent with this, activation of the iron regulon during calorie restriction (or the diauxic shift) has also been observed in two other articles:

https://doi.org/10.1016/S1016-8478(23)13999-9

https://doi.org/10.1074/jbc.M307447200

Taken together, these contradictory data might blur the proposed model and make it unclear how to reconcile the results.

We thank the reviewer for pointing this out. Upon further consideration, we have now removed all mention of this paper from our manuscript as it is irrelevant to our situation, because the mRNA abundance studies during CR or with and without Ssd1 were not performed in situations in which the iron regulon is even activated such as aging, so there would not be any opportunity to detect reduced transcript levels due to CR or Ssd1 presence. Also, none of these studies were performed with Ssd1 overexpression which is the situation we are examining.  Our data clearly show that Ssd1 overexpression and CR reduced / prevented, respectively, production of proteins from the iron regulon during aging.

We do not feel that the iron regulon being activated by nutrient depletion at the diauxic shift is a fair comparison to the situation in cells happily dividing during CR. The levels of nutrient deprivation used in those studies have profound effects including arresting cell growth, activating autophagy, altering metabolism. The levels of CR that we use (0.05% glucose) does not activate any of these changes nor the iron regulon in young cells or old cells (Fig. 4).  

Reviewer #1 (Recommendations for the authors):

(1) The role of Ssd1 condensate formation in mRNA sequestration and lifespan expansion remains unclear. Thus, the study involves two parts (Ssd1 condensate formation and lifespan expansion via limiting Fe2+ accumulation), which are poorly linked. The study will therefore benefit from further data linking the two aspects.

Future experiments are planned to determine what mRNAs reside in the age-induced Ssd1 overexpression condensates, to determine if they include the iron regulon transcripts. This will require us to optimize isolation of old cells and isolation of the Ssd1 condensates from them, and is beyond the scope of the present study.

(2) The beneficial effects of Ssd1 overexpression and calorie restriction (CR) on lifespan are epistatic, yet the claim that both experimental conditions act via the same pathway should be further documented. It is recommended to combine Ssd1 overexpression with a well-defined condition that expands lifespan through a mechanism not involving changes in Fe2+ levels. A further increase in lifespan upon combining such conditions would at least indirectly support the authors' claim.

We have more than epistatic evidence to indicate that Ssd1 overexpression and CR are in the same pathway. Ssd1 overexpression and CR result in failure to properly induce the iron regulon during aging and subsequent reduced levels of iron, resulting in lifespan extension, supporting that they act via the same pathway. We do appreciate the point though and epistasis analyses are on our list for future studies.

(3) It is highly recommended to analyze ssd1 knockout cells: Is the shortened lifespan caused by intracellular Fe2+ accumulation, as predicted by the model? Does the knockout lead to an overactivation of the iron regulon? Such analysis will also document the physiological relevance of authentic Ssd1 levels in controlling yeast lifespan. The authors could test this possibility by determining intracellular Fe2+ levels (as done in Figure 5) and testing whether the mutant cells are partially rescued by the presence of an iron chelator (as done in Figure 5C).

We don’t think the normal role of Ssd1 is to sequester the iron regulon mRNAs to prevent its activation, given that wild type yeast with endogenous Ssd1 activates the iron regulon during aging. Rather, the failure to activate the iron regulon during aging is unique to when Ssd1 is overexpressed not at endogenous Ssd1 levels. As such, it may not be the case that the short lifespan of ssd1 yeast is due to iron accumulation (if that happens); yeast lacking SSD1 also have cell wall biogenesis problems and the defects in cell wall biogenesis shorten the replicative lifespan (Molon et al., Biogerentology 2018  PMID 29189912). 

(4) Figure 4: The authors could not analyze the impact of Ssd1 overexpression on the localization of GFP-Aft1 due to synthetic sickness. This was not observed under calorie restriction (CR) conditions and is therefore unexpected. Why should Ssd1 overexpression and CR have such diverse impacts on cellular physiology when combined with GFP-Aft1? Isn`t that observation arguing against CR and increased Ssd1 levels acting through the same pathway? A further clarification of this point is necessary.

Without further experimentation, we can only speculate that cellular changes that are unique to overexpression of Ssd1 and not shared with CR cause a negative interaction with GFP-Aft1. Of note, Aft1 has functions in addition to its role in activating the iron regulon (aft1∆ strains have a growth defect independent from its role in iron regulon activation [27]) and we have shown previously that overexpressed Ssd1 has a reduction in global protein translation. Future experiments would be necessary to delineate the basis for this synthetic sickness.

(5) Lowering Fe2+ levels upon Ssd1 overexpression is predicted to reduce oxidative stress. It is suggested to determine ROS levels upon Ssd1 overexpression to bolster that point.

This is a great suggestion. The lowering of Fe2+ in the Ssd1 mutants is something that happens at the end of the lifespan and therefore we would need to do experiments to detect reduced ROS using a live dye on our microfluidics platform. We are not aware of any live fluorescent reporters of ROS.  

Reviewer #2 (Recommendations for the authors):

(1) Page 6, 7th line of Replicative lifespan analyses, there is a double bracket.

This has been corrected. Thank you

(2) Page 18, line 6 of "failure to activate..." section, "revered" should be replaced with "reversed".

This has been corrected. Thank you

(3) Page 23, fix writing on line 2 of "Effects of CR..." section.

This has been corrected. Thank you

(4) Page 24, Author contributions section, replace "performed devised" with "designed".

This has been corrected. Thank you

Reviewer #3 (Recommendations for the authors):

(1) Figure 3C: The panel legend is somewhat confusing due to the color scheme and the scattering of labels across panels. A more consistent labeling strategy would help readability.

We agree, and the labelling has now been improved. Thank you. 

(2) Figure 3D vs Figure 3B: it appears that Fit2 activation occurs substantially earlier than Aft1 translocation, which reduces the predictive value of Fit2 compared to Aft1. This is puzzling given that Fit2 is expected to be a direct target of Aft1. Could this discrepancy be related to the thresholding used for Fit2-mCherry display? The color scale in Figure 3D is also somewhat misleading, as most of the segments appear greenish. A continuous color gradient, perhaps restricted to the [10-120] interval, might give a clearer picture of iron regulon activation.

For the Aft1-mcherry experiment, we are only able to accurately annotate nuclear localization when Aft1 has been fully (or mostly) translocated into the nucleus from the cytoplasm such that this data is likely to be on the conservative side. However, activation of the iron regulon likely occurs as Aft1 is translocated into the nucleolus, so a minimal initial amount of Aft1 (for which we don’t have enough resolution in this system to detect) could be enough for FIT2 and ARN1 induction.  By contrast, the Fit2 and Arn1 signal is measuring increase over a background of nothing, so is very easy to detect even at low level induction. To allow the readers to see all our data without over thresholding, we prefer to present the induction of Fit2 and Arn1 at all intensity levels even the very low level induction (green).

(3) "In control strains, expression of Fit2 and Arn1 varied across the population, but generally increased with age": for the right panel, normalization might be more appropriate. What is the fold change in fluorescence during lifespan? Reporting ΔmCherry intensity alone does not provide a quantitative measure of induction.

We have changed the figure to show quantitation as fold change, as suggested.

(4) Figure 6 (model): The model figure is conceptually useful but not easy to follow in its current form; a revised schematic with a clearer depiction of the pathway activations at different replicative ages would be helpful.

We have changed the figure to make the model more clear, as suggested.

Author response:

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

Reviewer #1 (Public Review):

Summary:

Crohn's disease is a prevalent inflammatory bowel disease that often results in patient relapse post anti-TNF blockades. This study employs a multifaceted approach utilizing single-cell RNA sequencing, flow cytometry, and histological analyses to elucidate the cellular alterations in pediatric Crohn's disease patients pre and post-anti-TNF treatment and comparing them with non-inflamed pediatric controls. Utilizing an innovative clustering approach, the research distinguishes distinct cellular states that signify the disease's progression and response to treatment. Notably, the study suggests that the anti-TNF treatment pushes pediatric patients towards a cellular state resembling adult patients with persistent relapses. This study's depth offers a nuanced understanding of cell states in CD progression that might forecast the disease trajectory and therapy response.

Robust Data Integration: The authors adeptly integrate diverse data types: scRNA-seq, histological images, flow cytometry, and clinical metadata, providing a holistic view of the disease mechanism and response to treatment.

Novel Clustering Approach: The introduction and utilization of ARBOL, a tiered clustering approach, enhances the granularity and reliability of cell type identification from scRNA-seq data.

Clinical Relevance: By associating scRNA-seq findings with clinical metadata, the study offers potentially significant insights into the trajectory of disease severity and anti-TNF response; which might help with the personalized treatment regimens.

Treatment Dynamics: The transition of the pediatric cellular ecosystem towards an adult, more treatment-refractory state upon anti-TNF treatment is a significant finding. It would be beneficial to probe deeper into the temporal dynamics and the mechanisms underlying this transition.

Comparative Analysis with Adult CD: The positioning of on-treatment biopsies between treatment-naïve pediCD and on-treatment adult CD is intriguing. A more in-depth exploration comparing pediatric and adult cellular ecosystems could provide valuable insights into disease evolution.

Areas of improvement:

(1) The legends accompanying the figures are quite concise. It would be beneficial to provide a more detailed description within the legends, incorporating specifics about the experiments conducted and a clearer representation of the data points. 

We agree that it is beneficial to have descriptive figure legends that balance elements of experimental design, methodology, and statistical analyses employed in order to have a clear understanding throughout the manuscript. We have gone through and clarified areas throughout.  

(2) Statistical significance is missing from Fig. 1c WBC count plot, Fig. 2 b-e panels. Please provide it even if it's not significant. Also, the legend should have the details of stat test used.

We have now added details of statistical significance data in the Figure 1 legends. Please note that Mann-Whitney U-test was used for clinical categorical data.

(3) In the study, the NOA group is characterized by patients who, after thorough clinical evaluations, were deemed to exhibit milder symptoms, negating the need for anti-TNF prescriptions. This mild nature could potentially align the NOA group closer to FGID-a condition intrinsically defined by its low to non-inflammatory characteristics. Such an alignment sparks curiosity: is there a marked correlation between these two groups? A preliminary observation suggesting such a relationship can be spotted in Figure 6, particularly panels A and B. Given the prevalence of FGID among the pediatric population, it might be prudent for the authors to delve deeper into this potential overlap, as insights gained from mild-CD cases could provide valuable information for managing FGID.

Thank you for this insightful point. On histopathology and endoscopy, the NOA exhibited microscopic and macroscopic inflammation which landed these patients with the CD diagnosis, albeit mild on both micro and macro accounts. By contrast, the FGID group by definition will not have inflammation of microscopic and macroscopic evaluation. There is great interest in the field of adult and pediatric gastroenterology to understand why patients develop symptoms without evidence of inflammation. However, in 2023 the diagnostic tools of endoscopy with biopsy and histopathology is not sensitive enough to detect transcript level inflammation, positioning single-cell technology to be able to reveal further information in both disease processes.

Based on the reviewer’s suggestions, we have calculated a heatmap of overlapping NOA and FGID cell states along the Figure 6a joint-PC1, showing where NOA CD patients and FGID patients overlap in terms of cell states. This is displayed in Supplemental Figure 15d. This revealed a set of T, Myeloid, and Epithelial cell states that were most important in describing variance along the FGID-CD axis, allowing us to hone in on similarities at the boundary between FGID and CD. By comparing the joint cell states with CD atlas curated cluster names, we identified CCR7-expressing T cell states and GSTA2-expressing epithelial states associated with this overlap. 

(4) Furthermore, Figure 7 employs multi-dimensional immunofluorescence to compare CD, encompassing all its subtypes, with FGID. If the data permits, subdividing CD into PR, FR, and NOA for this comparison could offer a more nuanced understanding of the disease spectrum. Such a granular perspective is invaluable for clinical assessments. The key question then remains: do the sample categorizations for the immunofluorescence study accommodate this proposed stratification?

Thank you for the thoughtful discussion. We agree that stratifying Crohn’s disease by PR, FR, and NOA would provide valuable clinical insight. Unfortunately our multiplex IF cohort was designed to maximize overall CD versus FGID comparisons and does not contain enough samples in patient subgroups to power such an analysis. We have highlighted this limitation in the text.  

(5)The study's most captivating revelation is the proximity of anti-TNF-treated pediatric CD (pediCD) biopsies to adult treatment-refractory CD. Such an observation naturally raises the question: How does this alignment compare to a standard adult colon, and what proportion of this similarity is genuinely disease-specific versus reflective of an adult state? To what degree does the similarity highlight disease-specific traits?

Delving deeper, it will be of interest to see whether anti-TNF treatment is nudging the transcriptional state of the cells towards a more mature adult stage or veering them into a treatment-resistant trajectory. If anti-TNF therapy is indeed steering cells toward a more adult-like state, it might signify a natural maturation process; however, if it's directing them toward a treatment-refractory state, the long-term therapeutic strategies for pediatric patients might need reconsideration.

Thank you to the reviewer for another insightful point. We agree that age-matched samples are critical to evaluate disease cell states and hence we have age-matched controls in our pediatric cohort. Our timeline of follow-up only spans 3 years and patients remain in the pediatric age range at times of follow-up endoscopy and biopsy and would not be reflective of an adult GI state. We believe that the cellular behavior from naïve to treatment biopsy to on treatment biopsy is reflective of disease state rather than movement towards and adult-like state. We would also like to point out that pediatric onset IBD (Crohn’s and ulcerative colitis) traditionally has been harder to treat and presents with more extensive disease state (PMID: 22643596) and the ability to detect need for therapy escalation/change would be an invaluable tool for clinicians.  

We share the reviewer’s interest in disentangling a natural maturation process from disease and treatment-specific changes. Because the patients who were not given treatment did not move towards the adult-like phenotype, it could point to a push towards a treatment-resistant trajectory. To further support these findings, we generated a new disease-pseudotime figure Supplemental Figure 17, using cross-validation methods and the TradeSeq package. This figure was designed to track how each pediatric sample shifts from the treatment-naïve state through antiTNF therapy and to test the robustness of these shifts across samples. The new visualizations show patterns that do not recapitulate natural aging processes but rather shifts across all cell types associated with antiTNF treatment.

Reviewer #2 (Public Review):

Summary:

Through this study, the authors combine a number of innovative technologies including scRNAseq to provide insight into Crohn's disease. Importantly samples from pediatric patients are included. The authors develop a principled and unbiased tiered clustering approach, termed ARBOL. Through high-resolution scRNAseq analysis the authors identify differences in cell subsets and states during pediCD relative to FGID. The authors provide histology data demonstrating T cell localisation within the epithelium. Importantly, the authors find anti-TNF treatment pushes the pediatric cellular ecosystem toward an adult state.

Strengths:

This study is well presented. The introduction clearly explains the important knowledge gaps in the field, the importance of this research, the samples that are used, and study design.

The results clearly explain the data, without overstating any findings. The data is well presented. The discussion expands on key findings and any limitations to the study are clearly explained.

I think the biological findings from, and bioinformatic approach used in this study, will be of interest to many and significantly add to the field.

Weaknesses:

(1) The ARBOL approach for iterative tiered clustering on a specific disease condition was demonstrated to work very well on the datasets generated in this study where there were no obvious batch effects across patients. What if strong batch effects are present across donors where PCA fails to mitigate such effects? Are there any batch correction tools implemented in ARBOL for such cases?

We thank the reviewer for their insightful point, the full extent to which ARBOL can address batch effects requires further study. To this end we integrated Harmony into the ARBOL architecture and used it in the paper to integrate a previous study with the data presented (Figure 8). We have added to ARBOL’s github README how to use Harmony with the automated clustering method. With ARBOL, as well as traditional clustering methods, batch effects can cause artifactual clustering at any tier of clustering. Due to iteration, this can cause batch effects to present themselves in a single round of clustering, followed by further rounds of clustering that appear highly similar within each batch subset. Harmony addresses this issue, removing these batch-related clustering rounds. The later arrangement of fine-grained clusters using the bottom-up approach can use the batch-corrected latent space to calculate relationships between cell states, removing the effects from both sides of the algorithm. As stated, the extent to which ARBOL can be used to systematically address these batch effects requires further research, but the algorithmic architecture of ARBOL is well suited to address these effects.

(2) The authors mentioned that the clustering tree from the recursive sub-clustering contained too much noise, and they therefore used another approach to build a hierarchical clustering tree for the bottom-level clusters based on unified gene space. But in general, how consistent are these two trees?

Thank you for this thoughtful question. The two tree methodologies are not consistent due to their algorithmic differences, but both are important for several reasons: 

(1) The clustering tree is top-down, meaning low resolution lineage-related clusters are calculated first. Doublets and quality differences can cause very small clusters of different lineages (endothelial vs fibroblast) to fall under the incorrect lineage at first in the sub clustering tree, but these are recaptured during further sub clustering rounds, and then disentangled by the cluster-centroid tree.

(2) The hierarchical tree is a rose tree, meaning each branching point can contain several daughter branches, while taxonomies based on distances between species (or cell types in this case) are binary trees with only 2 branches per branching point, because distances between each cluster are unique. Because this taxonomy, or bottom-up, is different from the top-down approach, it is useful to then look at how these bottom-level clusters are similar. To that end, we performed pair-wise differential expression between all end clusters and clustered based on those genes. 

(3) Calculation of a binary tree represents a quantitative basis for comparing the transcriptomic distance between clusters as opposed to relying on distances calculated within a heuristic manifold such as UMAP or algorithmic similarity space such as cluster definitions based on KNN graphs.

In practice, this dual view rescues small clusters that may have been mis-grouped by technical artifacts and gives a quantitative distance based hierarchy that can be compared across metadata covariates.

Reviewer #1 (Public review):

Summary:

This paper reports model simulations and a human behavioral experiment studying predictive learning in a multidimensional environment. The authors claim that semantic biases help people resolve ambiguity about predictive relationships due to spurious correlations.

Strengths:

(1) The general question addressed by the paper is important.

(2) The paper is clearly written.

(3) Experiments and analyses are rigorously executed.

Weaknesses:

(1) Showing that people can be misled by spurious correlations, and that they can overcome this to some extent by using semantic structure, is not especially surprising to me. Related literature already exists on illusory correlation, illusory causation, superstitious behavior, and inductive biases in causal structure learning. None of this work features in the paper, which is rather narrowly focused on a particular class of predictive representations, which, in fact, may not be particularly relevant for this experiment. I also feel that the paper is rather long and complex for what is ultimately a simple point based on a single experiment.

(2) Putting myself in the shoes of an experimental subject, I struggled to understand the nature of semantic congruency. I don't understand why the builder and terminal robots should have similar features is considered a natural semantic inductive bias. Humans build things all the time that look different from them, and we build machines that construct artifacts that look different from the machines. I think the fact that the manipulation worked attests to the ability of human subjects to pick up on patterns rather than supporting the idea that this reflects an inductive bias they brought to the experiment.

(3) As the authors note, because the experiment uses only a single transition, it's not clear that it can really test the distinctive aspects of the SR/SF framework, which come into play over longer horizons. So I'm not really sure to what extent this paper is fundamentally about SFs, as it's currently advertised.

(4) One issue with the inductive bias as defined in Equation 15 is that I don't think it will converge to the correct SR matrix. Thus, the bias is not just affecting the learning dynamics, but also the asymptotic value (if there even is one; that's not clear either). As an empirical model, this isn't necessarily wrong, but it does mess with the interpretation of the estimator. We're now talking about a different object from the SR.

(5) Some aspects of the empirical and model-based results only provide weak support for the proposed model. The following null effects don't agree with the predictions of the model:

(a) No effect of condition on reward.

(b) No effect of condition on composition spurious predictiveness.

(c) No effect of condition on the fitted bias parameter. The authors present some additional exploratory analyses that they use to support their claims, but this should be considered weaker support than the results of preregistered analyses.

(6) I appreciate that the authors were transparent about which predictions weren't confirmed. I don't think they're necessarily deal-breakers for the paper's claims. However, these caveats don't show up anywhere in the Discussion.

(7) I also worry that the study might have been underpowered to detect some of these effects. The preregistration doesn't describe any pilot data that could be used to estimate effect sizes, and it doesn't present any power analysis to support the chosen sample sizes, which I think are on the small side for this kind of study.

B&GN appreciate Smith’s contribution and agree on the importance of combining typology with cognitive experiments. Nevertheless, Smith talked about two types of mismatch between typological and experimental results, while B&GN say that there are many more possible explanations for mismatch (they list the methodological problems in both approaches). B&GN think we cannot blindly trust typological results yet, cause they can be uncertain.

According to Smith, analyses of typological data can be a source of potential hypotheses about the mechanisms shaping linguistic systems, but it cannot speak to those causal mechanisms. Here lies the value of experimental work —-> test cognitive and interactional mechanisms that may be the potential cause for universals.for this reason, unlike B&GN, Smith thinks this data shouldn’t be used only to test the robustness of the results about the same phenomenon.

Author response:

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

I thank the authors for their clarifications. The manuscript is much improved now, in my opinion. The new power spectral density plots and revised Figure 1 are much appreciated. However, there is one remaining point that I am unclear about. In the rebuttal, the authors state the following: "To directly address the question of whether the auditory signal was distracting, we conducted a follow-up MEG experiment. In this study, we observed a significant reduction in visual accuracy during the second block when the distractor was present (see Fig. 7B and Suppl. Fig. 1B), providing clear evidence of a distractor cost under conditions where performance was not saturated." 

I am very confused by this statement, because both Fig. 7B and Suppl. Fig. 1B show that the visual- (i.e., visual target presented alone) has a lower accuracy and longer reaction time than visual+ (i.e., visual target presented with distractor). In fact, Suppl. Fig. 1B legend states the following: "accuracy: auditory- - auditory+: M = 7.2 %; SD = 7.5; p = .001; t(25) = 4.9; visual- - visual+: M = -7.6%; SD = 10.80; p < .01; t(25) = -3.59; Reaction time: auditory- - auditory +: M = -20.64 ms; SD = 57.6; n.s.: p = .08; t(25) = -1.83; visual- - visual+: M = 60.1 ms ; SD = 58.52; p < .001; t(25) = 5.23)." 

These statements appear to directly contradict each other. I appreciate that the difficulty of auditory and visual trials in block 2 of MEG experiments are matched, but this does not address the question of whether the distractor was actually distracting (and thus needed to be inhibited by occipital alpha). Please clarify.

We apologize for mixing up the visual and auditory distractor cost in our rebuttal. The reviewer is right in that our two statements contradict each other.

To clarify: In the EEG experiment, we see significant distractor cost for auditory distractors in the accuracy (which can be seen in SUPPL Fig. 1A). We also see a faster reaction time with auditory distractors, which may speak to intersensory facilitation. As we used the same distractors for both experiments, it can be assumed that they were distracting in both experiments.

In our follow-up MEG-experiment, as the reviewer stated, performance in block 2 was higher than in block 1, even though there were distractors present. In this experiment, distractor cost and learning effects are difficult to disentangle. It is possible that participants improved over time for the visual discrimination task in Block 1, as performance at the beginning was quite low. To illustrate this, we divided the trials of each condition into bins of 10 and plotted the mean accuracy in these bins over time (see Author response image 1). Here it can be seen that in Block 2, there is a more or less stable performance over time with a variation < 10 %. In Block 1, both for visual as well as auditory trials, an improvement over time can be seen. This is especially strong for visual trials, which span a difference of > 20%. Note that the mean performance for the 80-90 trial bin was higher than any mean performance observed in Block 2. 

Additionally, the same paradigm has been applied in previous investigations, which also found distractor costs for the here-used auditory stimuli in blocked and non-blocked designs. See:

Mazaheri, A., van Schouwenburg, M. R., Dimitrijevic, A., Denys, D., Cools, R., & Jensen, O. (2014). Region-specific modulations in oscillatory alpha activity serve to facilitate processing in the visual and auditory modalities. NeuroImage, 87, 356–362. https://doi.org/10.1016/j.neuroimage.2013.10.052

Van Diepen, R & Mazaheri, A 2017, 'Cross-sensory modulation of alpha oscillatory activity: suppression, idling and default resource allocation', European Journal of Neuroscience, vol. 45, no. 11, pp. 1431-1438. https://doi.org/10.1111/ejn.13570

Author response image 1.

Accuracy development over time in the MEG experiment. During block 1, a performance increase over time can be observed for visual as well as for auditory stimuli. During Block 2, performance is stable over time. Data are presented as mean ± SEM. N = 27 (one participant was excluded from this analysis, as their trial count in at least one condition was below 90 trials).

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

In this study, Brickwedde et al. leveraged a cross-modal task where visual cues indicated whether upcoming targets required visual or auditory discrimination. Visual and auditory targets were paired with auditory and visual distractors, respectively. The authors found that during the cue-to-target interval, posterior alpha activity increased along with auditory and visual frequency-tagged activity when subjects were anticipating auditory targets. The authors conclude that their results disprove the alpha inhibition hypothesis, and instead implies that alpha "regulates downstream information transfer." However, as I detail below, I do not think the presented data irrefutably disproves the alpha inhibition hypothesis. Moreover, the evidence for the alternative hypothesis of alpha as an orchestrator for downstream signal transmission is weak. Their data serves to refute only the most extreme and physiologically implausible version of the alpha inhibition hypothesis, which assumes that alpha completely disengages the entire brain area, inhibiting all neuronal activity.

We thank the reviewer for taking the time to provide additional feedback and suggestions and we improved our manuscript accordingly.

(1) Authors assign specific meanings to specific frequencies (8-12 Hz alpha, 4 Hz intermodulation frequency, 36 Hz visual tagging activity, 40 Hz auditory tagging activity), but the results show that spectral power increases in all of these frequencies towards the end of the cue-to-target interval. This result is consistent with a broadband increase, which could simply be due to additional attention required when anticipating auditory target (since behavioral performance was lower with auditory targets, we can say auditory discrimination was more difficult). To rule this out, authors will need to show a power spectral density curve with specific increases around each frequency band of interest. In addition, it would be more convincing if there was a bump in the alpha band, and distinct bumps for 4 vs 36 vs 40 Hz band.

This is an interesting point with several aspects, which we will address separately

Broadband Increase vs. Frequency-Specific Effects:

The suggestion that the observed spectral power increases may reflect a broadband effect rather than frequency-specific tagging is important. However, Supplementary Figure 11 shows no difference between expecting an auditory or visual target at 44 Hz. This demonstrates that (1) there is no uniform increase across all frequencies, and (2) the separation between our stimulation frequencies was sufficient to allow differentiation using our method.

Task Difficulty and Performance Differences:

The reviewer suggests that the observed effects may be due to differences in task difficulty, citing lower performance when anticipating auditory targets in the EEG study. This issue was explicitly addressed in our follow-up MEG study, where stimulus difficulty was calibrated. In the second block—used for analysis—accuracy between auditory and visual targets was matched (see Fig. 7B). The replication of our findings under these controlled conditions directly rules out task difficulty as the sole explanation. This point is clearly presented in the manuscript.

Power Spectrum Analysis:

The reviewer’s suggestion that our analysis lacks evidence of frequency-specific effects is addressed directly in the manuscript. While we initially used the Hilbert method to track the time course of power fluctuations, we also included spectral analyses to confirm distinct peaks at the stimulation frequencies. Specifically, when averaging over the alpha cluster, we observed a significant difference at 10 Hz between auditory and visual target expectation, with no significant differences at 36 or 40 Hz in that cluster. Conversely, in the sensor cluster showing significant 36 Hz activity, alpha power did not differ, but both 36 Hz and 40 Hz tagging frequencies showed significant effects These findings clearly demonstrate frequency-specific modulation and are already presented in the manuscript.

(2) For visual target discrimination, behavioral performance with and without the distractor is not statistically different. Moreover, the reaction time is faster with distractor. Is there any evidence that the added auditory signal was actually distracting?

We appreciate the reviewer’s observation regarding the lack of a statistically significant difference in behavioral performance for visual target discrimination with and without the auditory distractor. While this was indeed the case in our EEG experiment, we believe the absence of an accuracy effect may be attributable to a ceiling effect, as overall visual performance approached 100%. This high baseline likely masked any subtle influence of the distractor.

To directly address the question of whether the auditory signal was distracting, we conducted a follow-up MEG experiment. In this study, we observed a significant reduction in visual accuracy during the second block when the distractor was present (see Fig. 7B and Suppl. Fig. 1B), providing clear evidence of a distractor cost under conditions where performance was not saturated.

Regarding the faster reaction times observed in the presence of the auditory distractor, this phenomenon is consistent with prior findings on intersensory facilitation. Auditory stimuli, which are processed more rapidly than visual stimuli, can enhance response speed to visual targets—even when the auditory input is non-informative or nominally distracting (Nickerson, 1973; Diederich & Colonius, 2008; Salagovic & Leonard, 2021). Thus, while the auditory signal may facilitate motor responses, it can simultaneously impair perceptual accuracy, depending on task demands and baseline performance levels.

Taken together, our data suggest that the auditory signal does exert a distracting influence, particularly under conditions where visual performance is not at ceiling. The dual effect—facilitated reaction time but reduced accuracy—highlights the complexity of multisensory interactions and underscores the importance of considering both behavioral and neurophysiological measures.

(3) It is possible that alpha does suppress task-irrelevant stimuli, but only when it is distracting. In other words, perhaps alpha only suppresses distractors that are presented simultaneously with the target. Since the authors did not test this, they cannot irrefutably reject the alpha inhibition hypothesis.

The reviewer’s claim that we did not test whether alpha suppresses distractors presented simultaneously with the target is incorrect. As stated in the manuscript and supported by our data (see point 2), auditory distractors were indeed presented concurrently with visual targets, and they were demonstrably distracting. Therefore, the scenario the reviewer suggests was not only tested—it forms a core part of our design.

Furthermore, it was never our intention to irrefutably reject the alpha inhibition hypothesis. Rather, our aim was to revise and expand it. If our phrasing implied otherwise, we have now clarified this in the manuscript. Specifically, we propose that alpha oscillations:

(a) Exhibit cyclic inhibitory and excitatory dynamics;

(b) Regulate processing by modulating transfer pathways, which can result in either inhibition or facilitation depending on the network context.

In our study, we did not observe suppression of distractor transfer, likely due to the engagement of a supramodal system that enhances both auditory and visual excitability. This interpretation is supported by prior findings (e.g., Jacoby et al., 2012), which show increased visual SSEPs under auditory task load, and by Zhigalov et al. (2020), who found no trial-by-trial correlation between alpha power and visual tagging in early visual areas, despite a general association with attention.

Recent evidence (Clausner et al., 2024; Yang et al., 2024) further supports the notion that alpha oscillations serve multiple functional roles depending on the network involved. These roles include intra- and inter-cortical signal transmission, distractor inhibition, and enhancement of downstream processing (Scheeringa et al., 2012; Bastos et al., 2015; Zumer et al., 2014). We believe the most plausible account is that alpha oscillations support both functions, depending on context.

To reflect this more clearly, we have updated Figure 1 to present a broader signal-transfer framework for alpha oscillations, beyond the specific scenario tested in this study.

We have now revised Figure 1 and several sentences in the introduction and discussion, to clarify this argument.

L35-37: Previous research gave rise to the prominent alpha inhibition hypothesis, which suggests that oscillatory activity in the alpha range (~10 Hz) plays a mechanistic role in selective attention through functional inhibition of irrelevant cortical areas (see Fig. 1; Foxe et al., 1998; Jensen & Mazaheri, 2010; Klimesch et al., 2007).

L60-65: In contrast, we propose that functional and inhibitory effects of alpha modulation, such as distractor inhibition, are exhibited through blocking or facilitating signal transmission to higher order areas (Peylo et al., 2021; Yang et al., 2023; Zhigalov & Jensen, 2020; Zumer et al., 2014), gating feedforward or feedback communication between sensory areas (see Fig. 1; Bauer et al., 2020; Haegens et al., 2015; Uemura et al., 2021).

L482-485: This suggests that responsiveness of the visual stream was not inhibited when attention was directed to auditory processing and was not inhibited by occipital alpha activity, which directly contradicts the proposed mechanism behind the alpha inhibition hypothesis.

L517-519: Top-down cued changes in alpha power have now been widely viewed to play a functional role in directing attention: the processing of irrelevant information is attenuated by increasing alpha power in areas involved with processing this information (Foxe, Simpson, & Ahlfors, 1998; Hanslmayr et al., 2007; Jensen & Mazaheri, 2010).

L566-569: As such, it is conceivable that alpha oscillations can in some cases inhibit local transmission, while in other cases, depending on network location, connectivity and demand, alpha oscillation can facilitate signal transmission. This mechanism allows to increase transmission of relevant information and to block transmission of distractors.

(4) In the abstract and Figure 1, the authors claim an alternative function for alpha oscillations; that alpha "orchestrates signal transmission to later stages of the processing stream." In support, the authors cite their result showing that increased alpha activity originating from early visual cortex is related to enhanced visual processing in higher visual areas and association areas. This does not constitute a strong support for the alternative hypothesis. The correlation between posterior alpha power and frequency-tagged activity was not specific in any way; Fig. 10 shows that the correlation appeared on both 1) anticipating-auditory and anticipating-visual trials, 2) the visual tagged frequency and the auditory tagged activity, and 3) was not specific to the visual processing stream. Thus, the data is more parsimonious with a correlation than a causal relationship between posterior alpha and visual processing.

Again, the reviewer raises important points, which we want to address

The correlation between posterior alpha power and frequency-tagged activity was not specific, as it is present both when auditory and visual targets are expected:

If there is a connection between posterior alpha activity and higher-order visual information transfer, then it can be expected that this relationship remains across conditions and that a higher alpha activity is accompanied by higher frequency-tagged activity, both over trials and over conditions. However, it is possible that when alpha activity is lower, such as when expecting a visual target, the signal-to-noise ratio is affected, which may lead to higher difficulty to find a correlation effect in the data when using non-invasive measurements.

The connection between alpha activity and frequency-tagged activity appears both for auditory as well as visual stimuli and The correlation is not specific to the visual processing stream:

While we do see differences between conditions (e.g. in the EEG-analysis, mostly 36 Hz correlated with alpha activity and only in one condition 40 Hz showed a correlation as well), it is true that in our MEG analysis, we found correlations both between alpha activity and 36 Hz as well as alpha activity and 40 Hz.  

We acknowledge that when analysing frequency-tagged activity on a trial-by-trial basis, where removal of non-timelocked activity through averaging (which we did when we tested for condition differences in Fig. 4 and 9) is not possible, there is uncertainty in the data. Baseline-correction can alleviate this issue, but it cannot offset the possibility of non-specific effects. We therefore decided to repeat the analysis with a fast-fourier calculated power instead of the Hilbert power, in favour of a higher and stricter frequency-resolution, as we averaged over a time-period and thus, the time-domain was not relevant for this analysis. In this more conservative analysis, we can see that only 36 Hz tagged activity when expecting an auditory target correlated with early visual alpha activity.

Additionally, we added correlation analyses between alpha activity and frequency-tagged activity within early visual areas, using the sensor cluster which showed significant condition differences in alpha activity. Here, no correlations between frequency-tagged activity and alpha activity could be found (apart from a small correlation with 40 Hz which could not be confirmed by a median split; see SUPPL Fig. 14 C). The absence of a significant correlation between early visual alpha and frequency-tagged activity has previously been described by others (Zhigalov & Jensen, 2020) and a Bayes factor of below 1 also indicated that the alternative hypotheses is unlikely.

Nonetheless, a correlation with auditory signal is possible and could be explained in different ways. For example, it could be that very early auditory feedback in early visual cortex (see for example Brang et al., 2022) is transmitted alongside visual information to higher-order areas. Several studies have shown that alpha activity and visual as well as auditory processing are closely linked together (Bauer et al., 2020; Popov et al., 2023). Inference on whether or how this link could play out in the case of this manuscript expands beyond the scope of this study.

To summarize, we believe the fact that 36 Hz activity within early visual areas does not correlate with alpha activity on a trial-by-trial basis, but that 36 Hz activity in other areas does, provides strong evidence that alpha activity affects down-stream signal processing.

We mention this analysis now in our discussion:

L533-536: Our data provides evidence in favour of this view, as we can show that early sensory alpha activity does not covary over trials with SSEP magnitude in early visual areas, but covaries instead over trials with SSEP magnitude in higher order sensory areas (see also SUPPL. Fig. 14).

Reviewer #1 (Recommendations for the authors):

The evidence for the alternative hypothesis, that alpha in early sensory areas orchestrates downstream signal transmission, is not strong enough to be described up front in the abstract and Figure 1. I would leave it in the Discussion section, but advise against mentioning it in the abstract and Figure 1.

We appreciate the reviewer’s concern regarding the inclusion of the alternative hypothesis—that alpha activity in early sensory areas orchestrates downstream signal transmission—in the abstract and Figure 1. While we agree that this interpretation is still developing, recent studies (Keitel et al., 2025; Clausner et al., 2024; Yang et al., 2024) provide growing support for this framework.

In response, we have revised the introduction, discussion, and Figure 1 to clarify that our intention is not to outright dismiss the alpha inhibition hypothesis, but to refine and expand it in light of new data. This revision does not invalidate the prior literature on alpha timing and inhibition; rather, it proposes an updated mechanism that may better account for observed effects.

We have though retained Figure 1, as it visually contextualizes the broader theoretical landscape. while at the same time added further analyses to strengthen our empirical support for this emerging view.

References:

Bastos, A. M., Litvak, V., Moran, R., Bosman, C. A., Fries, P., & Friston, K. J. (2015). A DCM study of spectral asymmetries in feedforward and feedback connections between visual areas V1 and V4 in the monkey. NeuroImage, 108, 460–475. https://doi.org/10.1016/j.neuroimage.2014.12.081

Bauer, A. R., Debener, S., & Nobre, A. C. (2020). Synchronisation of Neural Oscillations and Cross-modal Influences. Trends in cognitive sciences, 24(6), 481–495. https://doi.org/10.1016/j.tics.2020.03.003

Brang, D., Plass, J., Sherman, A., Stacey, W. C., Wasade, V. S., Grabowecky, M., Ahn, E., Towle, V. L., Tao, J. X., Wu, S., Issa, N. P., & Suzuki, S. (2022). Visual cortex responds to sound onset and offset during passive listening. Journal of neurophysiology, 127(6), 1547–1563. https://doi.org/10.1152/jn.00164.2021

Clausner T., Marques J., Scheeringa R. & Bonnefond M (2024). Feature specific neuronal oscillations in cortical layers BioRxiv :2024.07.31.605816. https://doi.org/10.1101/2024.07.31.605816

Diederich, A., & Colonius, H. (2008). When a high-intensity "distractor" is better then a low-intensity one: modeling the effect of an auditory or tactile nontarget stimulus on visual saccadic reaction time. Brain research, 1242, 219–230. https://doi.org/10.1016/j.brainres.2008.05.081

Haegens, S., Nácher, V., Luna, R., Romo, R., & Jensen, O. (2011). α-Oscillations in the monkey sensorimotor network influence discrimination performance by rhythmical inhibition of neuronal spiking. Proceedings of the National Academy of Sciences of the United States of America, 108(48), 19377–19382. https://doi.org/10.1073/pnas.1117190108

Jacoby, O., Hall, S. E., & Mattingley, J. B. (2012). A crossmodal crossover: opposite effects of visual and auditory perceptual load on steady-state evoked potentials to irrelevant visual stimuli. NeuroImage, 61(4), 1050–1058. https://doi.org/10.1016/j.neuroimage.2012.03.040

Keitel, A., Keitel, C., Alavash, M., Bakardjian, K., Benwell, C. S. Y., Bouton, S., Busch, N. A., Criscuolo, A., Doelling, K. B., Dugue, L., Grabot, L., Gross, J., Hanslmayr, S., Klatt, L.-I., Kluger, D. S., Learmonth, G., London, R. E., Lubinus, C., Martin, A. E., … Kotz, S. A. (2025). Brain rhythms in cognition – controversies and future directions. ArXiv. https://doi.org/10.48550/arXiv.2507.15639

Nickerson R. S. (1973). Intersensory facilitation of reaction time: energy summation or preparation enhancement?. Psychological review, 80(6), 489–509. https://doi.org/10.1037/h0035437

Popov, T., Gips, B., Weisz, N., & Jensen, O. (2023). Brain areas associated with visual spatial attention display topographic organization during auditory spatial attention. Cerebral cortex (New York, N.Y. : 1991), 33(7), 3478–3489. https://doi.org/10.1093/cercor/bhac285

Salagovic, C. A., & Leonard, C. J. (2021). A nonspatial sound modulates processing of visual distractors in a flanker task. Attention, perception & psychophysics, 83(2), 800–809. https://doi.org/10.3758/s13414-020-02161-5

Scheeringa, R., Petersson, K. M., Kleinschmidt, A., Jensen, O., & Bastiaansen, M. C. (2012). EEG α power modulation of fMRI resting-state connectivity. Brain connectivity, 2(5), 254–264. https://doi.org/10.1089/brain.2012.0088

Spaak, E., Bonnefond, M., Maier, A., Leopold, D. A., & Jensen, O. (2012). Layer-specific entrainment of γ-band neural activity by the α rhythm in monkey visual cortex. Current biology : CB, 22(24), 2313–2318. https://doi.org/10.1016/j.cub.2012.10.020

Yang, X., Fiebelkorn, I. C., Jensen, O., Knight, R. T., & Kastner, S. (2024). Differential neural mechanisms underlie cortical gating of visual spatial attention mediated by alpha-band oscillations. Proceedings of the National Academy of Sciences of the United States of America, 121(45), e2313304121. https://doi.org/10.1073/pnas.2313304121

Zhigalov, A., & Jensen, O. (2020). Alpha oscillations do not implement gain control in early visual cortex but rather gating in parieto-occipital regions. Human brain mapping, 41(18), 5176–5186. https://doi.org/10.1002/hbm.25183

Zumer, J. M., Scheeringa, R., Schoffelen, J. M., Norris, D. G., & Jensen, O. (2014). Occipital alpha activity during stimulus processing gates the information flow to object-selective cortex. PLoS biology, 12(10), e1001965. https://doi.org/10.1371/journal.pbio.1001965

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

We would like to thank all the reviewers for their valuable comments and criticisms. We have thoroughly revised the manuscript and the resource to address all the points raised by the reviewers. Below, we provide a point-by-point response for the sake of clarity.

Reviewer #1

__Evidence, reproducibility and clarity __

Summary: This manuscript, "MAVISp: A Modular Structure-Based Framework for Protein Variant Effects," presents a significant new resource for the scientific community, particularly in the interpretation and characterization of genomic variants. The authors have developed a comprehensive and modular computational framework that integrates various structural and biophysical analyses, alongside existing pathogenicity predictors, to provide crucial mechanistic insights into how variants affect protein structure and function. Importantly, MAVISp is open-source and designed to be extensible, facilitating reuse and adaptation by the broader community.

Major comments: - While the manuscript is formally well-structured (with clear Introduction, Results, Conclusions, and Methods sections), I found it challenging to follow in some parts. In particular, the Introduction is relatively short and lacks a deeper discussion of the state-of-the-art in protein variant effect prediction. Several methods are cited but not sufficiently described, as if prior knowledge were assumed. OPTIONAL: Extend the Introduction to better contextualize existing approaches (e.g., AlphaMissense, EVE, ESM-based predictors) and clarify what MAVISp adds compared to each.

We have expanded the introduction on the state-of-the-art of protein variant effects predictors, explaining how MAVISp departs from them.

- The workflow is summarized in Figure 1(b), which is visually informative. However, the narrative description of the pipeline is somewhat fragmented. It would be helpful to describe in more detail the available modules in MAVISp, and which of them are used in the examples provided. Since different use cases highlight different aspects of the pipeline, it would be useful to emphasize what is done step-by-step in each.

We have added a concise, narrative description of the data flow for MAVISp, as well as improved the description of modules in the main text. We will integrate the results section with a more comprehensive description of the available modules, and then clarify in the case studies which modules were applied to achieve specific results.

OPTIONAL: Consider adding a table or a supplementary figure mapping each use case to the corresponding pipeline steps and modules used.

We have added a supplementary table (Table S2) to guide the reader on the modules and workflows applied for each case study

We also added Table S1 to map the toolkit used by MAVISp to collect the data that are imported and aggregated in the webserver for further guidance.

- The text contains numerous acronyms, some of which are not defined upon first use or are only mentioned in passing. This affects readability. OPTIONAL: Define acronyms upon first appearance, and consider moving less critical technical details (e.g., database names or data formats) to the Methods or Supplementary Information. This would greatly enhance readability.

We revised the usage of acronyms following the reviewer’s directions of defying them at first appearance.

• The code and trained models are publicly available, which is excellent. The modular design and use of widely adopted frameworks (PyTorch and PyTorch Geometric) are also strong points. However, the Methods section could benefit from additional detail regarding feature extraction and preprocessing steps, especially the structural features derived from AlphaFold2 models. OPTIONAL: Include a schematic or a table summarizing all feature types, their dimensionality, and how they are computed.

We thank the reviewer for noticing and praising the availability of the tools of MAVISp. Our MAVISp framework utilizes methods and scores that incorporate machine learning features (such as EVE or RaSP), but does not employ machine learning itself. Specifically, we do not use PyTorch and do not utilize features in a machine learning sense. We do extract some information from the AlphaFold2 models that we use (such as the pLDDT score and their secondary structure content, as calculated by DSSP), and those are available in the MAVISp aggregated csv files for each protein entry and detailed in the Documentation section of the MAVISp website.

• The section on transcription factors is relatively underdeveloped compared to other use cases and lacks sufficient depth or demonstration of its practical utility. OPTIONAL: Consider either expanding this section with additional validation or removing/postponing it to a future manuscript, as it currently seems preliminary.

We have removed this section and included a mention in the conclusions as part of the future directions.

Minor comments: - Most relevant recent works are cited, including EVE, ESM-1v, and AlphaFold-based predictors. However, recent methods like AlphaMissense (Cheng et al., 2023) could be discussed more thoroughly in the comparison.

We have revised the introduction to accommodate the proper space for this comparison.

• Figures are generally clear, though some (e.g., performance barplots) are quite dense. Consider enlarging font sizes and annotating key results directly on the plots.

We have revised Figure 2 and presented only one case study to simplify its readability. We have also changed Figure 3, whereas retained the other previous figures since they seemed less problematic.

• Minor typographic errors are present. A careful proofreading is highly recommended. Below are some of the issues I identified: Page 3, line 46: "MAVISp perform" -> "MAVISp performs" Page 3, line 56: "automatically as embedded" -> "automatically embedded" Page 3, line 57: "along with to enhance" -> unclear; please revise Page 4, line 96: "web app interfaces with the database and present" -> "presents" Page 6, line 210: "to investigate wheatear" -> "whether" Page 6, lines 215-216: "We have in queue for processing with MAVISp proteins from datasets relevant to the benchmark of the PTM module." -> unclear sentence; please clarify Page 15, line 446: "Both the approaches" -> "Both approaches" Page 20, line 704: "advantage of multi-core system" -> "multi-core systems"

We have done a proofreading of the entire article, including the points above

Significance

General assessment: the strongest aspects of the study are the modularity, open-source implementation, and the integration of structural information through graph neural networks. MAVISp appears to be one of the few publicly available frameworks that can easily incorporate AlphaFold2-based features in a flexible way, lowering the barrier for developing custom predictors. Its reproducibility and transparency make it a valuable resource. However, while the technical foundation is solid and the effort substantial, the scientific narrative and presentation could be significantly improved. The manuscript is dense and hard to follow in places, with a heavy use of acronyms and insufficient explanation of key design choices. Improving the descriptive clarity, especially in the early sections, would greatly enhance the impact of this work.

Advance

to the best of my knowledge, this is one of the first modular platforms for protein variant effect prediction that integrates structural data from AlphaFold2 with bioinformatic annotations and even clinical data in an extensible fashion. While similar efforts exist (e.g., ESMfold, AlphaMissense), MAVISp distinguishes itself through openness and design for reusability. The novelty is primarily technical and practical rather than conceptual.

Audience

this study will be of strong interest to researchers in computational biology, structural bioinformatics, and genomics, particularly those developing variant effect predictors or analyzing the impact of mutations in clinical or functional genomics contexts. The audience is primarily specialized, but the open-source nature of the tool may diffuse its use among more applied or translational users, including those working in precision medicine or protein engineering.

Reviewer expertise: my expertise is in computational structural biology, molecular modeling, and (rather weak) machine learning applications in bioinformatics. I am familiar with graph-based representations of proteins, AlphaFold2, and variant effects based on Molecular Dynamics simulations. I do not have any direct expertise in clinical variant annotation pipelines.

Reviewer #2

__Evidence, reproducibility and clarity __

Summary: The authors present a pipeline and platform, MAVISp, for aggregating, displaying and analysis of variant effects with a focus on reclassification of variants of uncertain clinical significance and uncovering the molecular mechanisms underlying the mutations.

Major comments: - On testing the platform, I was unable to look-up a specific variant in ADCK1 (rs200211943, R115Q). I found that despite stating that the mapped refseq ID was NP_001136017 in the HGVSp column, it was actually mapped to the canonical UniProt sequence (Q86TW2-1). NP_001136017 actually maps to Q86TW2-3, which is missing residues 74-148 compared to the -1 isoform. The Uniprot canonical sequence has no exact RefSeq mapping, so the HGVSp column is incorrect in this instance. This mapping issue may also affect other proteins and result in incorrect HGVSp identifiers for variants.

We would like to thank the reviewer for pointing out these inconsistencies. We have revised all the entries and corrected them. If needed, the history of the cases that have been corrected can be found in the closed issues of the GitHub repository that we use for communication between biocurators and data managers (https://github.com/ELELAB/mavisp_data_collection). We have also revised the protocol we follow in this regard and the MAVISp toolkit to include better support for isoform matching in our pipelines for future entries, as well as for the revision/monitoring of existing ones, as detailed in the Method Section. In particular, we introduced a tool, uniprot2refseq, which aids the biocurator in identifying the correct match in terms of sequence length and sequence identity between RefSeq and UniProt. More details are included in the Method Section of the paper. The two relevant scripts for this step are available at: https://github.com/ELELAB/mavisp_accessory_tools/

- The paper lacks a section on how to properly interpret the results of the MAVISp platform (the case-studies are helpful, but don't lay down any global rules for interpreting the results). For example: How should a variant with conflicts between the variant impact predictors be interpreted? Are specific indicators considered more 'reliable' than others?

We have added a section in Results to clarify how to interpret results from MAVISp in the most common use cases.

• In the Methods section, GEMME is stated as being rank-normalised with 0.5 as a threshold for damaging variants. On checking the data downloaded from the site, GEMME was not rank-normalised but rather min-max normalised. Furthermore, Supplementary text S4 conflicts with the methods section over how GEMME scores are classified, S4 states that a raw-value threshold of -3 is used.

We thank the reviewer for spotting this inconsistency. This part in the main text was left over from a previous and preliminary version of the pre-print, we have revised the main text. Supplementary Text S4 includes the correct reference for the value in light of the benchmarking therewithin.

• Note. This is a major comment as one of the claims is that the associated web-tool is user-friendly. While functional, the web app is very awkward to use for analysis on any more than a few variants at once. The fixed window size of the protein table necessitates excessive scrolling to reach your protein-of-interest. This will also get worse as more proteins are added. Suggestion: add a search/filter bar. The same applies to the dataset window.

We have changed the structure of the webserver in such a way that now the whole website opens as its own separate window, instead of being confined within the size permitted by the website at DTU. This solves the fixed window size issue. Hopefully, this will improve the user experience.

We have refactored the web app by adding filtering functionality, both for the main protein table (that can now be filtered by UniProt AC, gene name or RefSeq ID) and the mutations table. Doing this required a general overhaul of the table infrastructure (we changed the underlying engine that renders the tables).

• You are unable to copy anything out of the tables.
• Hyperlinks in the tables only seem to work if you open them in a new tab or window.

The table overhauls fixed both of these issues

• All entries in the reference column point to the MAVISp preprint even when data from other sources is displayed (e.g. MAVE studies).

We clarified the meaning of the reference column in the Documentation on the MAVISp website, as we realized it had confused the reviewer. The reference column is meant to cite the papers where the computationally-generated MAVISp data are used, not external sources. Since we also have the experimental data module in the most recent release, we have also refactored the MAVISp website by adding a “Datasets and metadata” page, which details metadata for key modules. These include references to data from external sources that we include in MAVISp on a case-by-case basis (for example the results of a MAVE experiment). Additionally, we have verified that the papers using MAVISp data are updated in https://elelab.gitbook.io/mavisp/overview/publications-that-used-mavisp-data and in the csv file of the interested proteins.

Here below the current references that have been included in terms of publications using MAVISp data:

SMPD1

ASM variants in the spotlight: A structure-based atlas for unraveling pathogenic mechanisms in lysosomal acid sphingomyelinase

Biochim Biophys Acta Mol Basis Dis

38782304

https://doi.org/10.1016/j.bbadis.2024.167260

TRAP1

Point mutations of the mitochondrial chaperone TRAP1 affect its functions and pro-neoplastic activity

Cell Death & Disease

40074754

https://doi.org/10.1038/s41419-025-07467-6

BRCA2

Saturation genome editing-based clinical classification of BRCA2 variants

Nature

39779848

0.1038/s41586-024-08349-1

TP53, GRIN2A, CBFB, CALR, EGFR

TRAP1 S-nitrosylation as a model of population-shift mechanism to study the effects of nitric oxide on redox-sensitive oncoproteins

Cell Death & Disease

37085483

10.1038/s41419-023-05780-6

KIF5A, CFAP410, PILRA, CYP2R1

Computational analysis of five neurodegenerative diseases reveals shared and specific genetic loci

Computational and Structural Biotechnology Journal

38022694

https://doi.org/10.1016/j.csbj.2023.10.031

KRAS

Combining evolution and protein language models for an interpretable cancer driver mutation prediction with D2Deep

Brief Bioinform

39708841

https://doi.org/10.1093/bib/bbae664

OPTN

Decoding phospho-regulation and flanking regions in autophagy-associated short linear motifs

Communications Biology

40835742

10.1038/s42003-025-08399-9

DLG4,GRB2,SMPD1

Deciphering long-range effects of mutations: an integrated approach using elastic network models and protein structure networks

JMB

40738203

doi: 10.1016/j.jmb.2025.169359

Entering multiple mutants in the "mutations to be displayed" window is time-consuming for more than a handful of mutants. Suggestion: Add a box where multiple mutants can be pasted in at once from an external document.

During the table overhaul, we have revised the user interface to add a text box that allows free copy-pasting of mutation lists. While we understand having a single input box would have been ideal, the former selection interface (which is also still available) doesn’t allow copy-paste. This is a known limitation in Streamlit.

Minor comments

• Grammar. I appreciate that this manuscript may have been compiled by a non-native English speaker, but I would be remiss not to point out that there are numerous grammar errors throughout, usually sentence order issues or non-pluralisation. The meaning of the authors is mostly clear, but I recommend very thoroughly proof-reading the final version.

We have done proofreading on the final version of the manuscript

• There are numerous proteins that I know have high-quality MAVE datasets that are absent in the database e.g. BRCA1, HRAS and PPARG.

Yes, we are aware of this. It is far from trivial to properly import the datasets from multiplex assays. They often need to be treated on a case-by-case basis. We are in the process of carefully compiling locally all the MAVE data before releasing it within the public version of the database, so this is why they are missing. We are giving priorities to the ones that can be correlated with our predictions on changes in structural stability and then we will also cover the rest of the datasets handling them in batches. Having said this, we have checked the dataset for BRCA1, HRAS, and PPARG. We have imported the ones for PPARG and BRCA1 from ProtGym, referring to the studies published in 10.1038/ng.3700 and 10.1038/s41586-018-0461-z, respectively. Whereas for HRAS, checking in details both the available data and literature, while we did identify a suitable dataset (10.7554/eLife.27810), we struggled to understand what a sensible cut-off for discriminating between pathogenic and non-pathogenic variants would be, and so ended up not including it in the MAVISp dataset for now. We will contact the authors to clarify which thresholds to apply before importing the data.

• Checking one of the existing MAVE datasets (KRAS), I found that the variants were annotated as damaging, neutral or given a positive score (these appear to stand-in for gain-of-function variants). For better correspondence with the other columns, those with positive scores could be labelled as 'ambiguous' or 'uncertain'.

In the KRAS case study presented in MAVISP, we utilized the protein abundance dataset reported in (http://dx.doi.org/10.1038/s41586-023-06954-0) and made available in the ProteinGym repository (specifically referenced at https://github.com/OATML-Markslab/ProteinGym/blob/main/reference_files/DMS_substitutions.csv#L153). We adopted the precalculated thresholds as provided by the ProteinGym authors. In this regard, we are not really sure the reviewer is referring to this dataset or another one on KRAS.

• Numerous thresholds are defined for stabilizing / destabilizing / neutral variants in both the STABILITY and the LOCAL_INTERACTION modules. How were these thresholds determined? I note that (PMC9795540) uses a ΔΔG threshold of 1/-1 for defining stabilizing and destabilizing variants, which is relatively standard (though they also say that 2-3 would likely be better for pinpointing pathogenic variants).

We improved the description of our classification strategies for both modules in the Documentation page of our website. Also, we explained more clearly the possible sources of ‘uncertain’ annotations for the two modules in both the web app (Documentation page) and main text. Briefly, in the STABILITY module, we consider FoldX and either Rosetta or RaSP to achieve a final classification. We first classify one and the other independently, according to the following strategy:

If DDG ≥ 3, the mutation is Destabilizing If DDG ≤ −3, the mutation is Stabilizing If −2 We then compare the classifications obtained by the two methods: if they agree, then that is the final classification, if they disagree, then the final classification is Uncertain. The thresholds were selected based on a previous study, in which variants with changes in stability below 3 kcal/mol were not featuring a markedly different abundance at cellular level [10.1371/journal.pgen.1006739, 10.7554/eLife.49138]

Regarding the LOCAL_INTERACTION module, it works similarly as for the Stability module, in that Rosetta and FoldX are considered independently, and an implicit classification is performed for each, according to the rules (values in kcal/mol)

If DDG > 1, the mutation is Destabilizing. If DDG Each mutation is therefore classified for both methods. If the methods agree (i.e., if they classify the mutation in the same way), their consensus is the final classification for the mutation; if they do not agree, the final classification will be Uncertain.

If a mutation does not have an associated free energy value, the relative solvent accessible area is used to classify it: if SAS > 20%, the mutation is classified as Uncertain, otherwise it is not classified.

Thresholds here were selected according to best practices followed by the tool authors and more in general in the literature, as the reviewer also noticed.

• "Overall, with the examples in this section, we illustrate different applications of the MAVISp results, spanning from benchmarking purposes, using the experimental data to link predicted functional effects with structural mechanisms or using experimental data to validate the predictions from the MAVISp modules."

The last of these points is not an application of MAVISp, but rather a way in which external data can help validate MAVISp results. Furthermore, none of the examples given demonstrate an application in benchmarking (what is being benchmarked?).

We have revised the statements to avoid this confusion in the reader.

• Transcription factors section. This section describes an intended future expansion to MAVISp, not a current feature, and presents no results. As such, it should be moved to the conclusions/future directions section.

We have removed this section and included a mention in the conclusions as part of the future directions.

• Figures. The dot-plots generated by the web app, and in Figures 4, 5 and 6 have 2 legends. After looking at a few, it is clear that the lower legend refers to the colour of the variant on the X-axis - most likely referencing the ClinVar effect category. This is not, however, made clear either on the figures or in the app.

The reviewer’s interpretation on the second legend is correct - it does refer to the ClinVar classification. Nonetheless, we understand the positioning of the legend makes understanding what the legend refers to not obvious. We also revised the captions of the figures in the main text. On the web app, we have changed the location of the figure legend for the ClinVar effect category and added a label to make it clear what the classification refers to.

• "We identified ten variants reported in ClinVar as VUS (E102K, H86D, T29I, V91I, P2R, L44P, L44F, D56G, R11L, and E25Q, Fig.5a)" E25Q is benign in ClinVar and has had that status since first submitted.

We have corrected this in the text and the statements related to it.

Significance

Platforms that aggregate predictors of variant effect are not a new concept, for example dbNSFP is a database of SNV predictions from variant effect predictors and conservation predictors over the whole human proteome. Predictors such as CADD and PolyPhen-2 will often provide a summary of other predictions (their features) when using their platforms. MAVISp's unique angle on the problem is in the inclusion of diverse predictors from each of its different moules, giving a much wider perspective on variants and potentially allowing the user to identify the mechanistic cause of pathogenicity. The visualisation aspect of the web app is also a useful addition, although the user interface is somewhat awkward. Potentially the most valuable aspect of this study is the associated gitbook resource containing reports from biocurators for proteins that link relevant literature and analyse ClinVar variants. Unfortunately, these are only currently available for a small minority of the total proteins in the database with such reports. For improvement, I think that the paper should focus more on the precise utility of the web app / gitbook reports and how to interpret the results rather than going into detail about the underlying pipeline.

We appreciate the interest in the gitbook resource that we also see as very valuable and one of the strengths of our work. We have now implemented a new strategy based on a Python script introduced in the mavisp toolkit to generate a template Markdown file of the report that can be further customized and imported into GitBook directly (​​https://github.com/ELELAB/mavisp_accessory_tools/). This should allow us to streamline the production of more reports. We are currently assigning proteins in batches for reporting to biocurator through the mavisp_data_collection GitHub to expand their coverage. Also, we revised the text and added a section on the interpretation of results from MAVISp. with a focus on the utility of the web-app and reports.

In terms of audience, the fast look-up and visualisation aspects of the web-platform are likely to be of interest to clinicians in the interpretation of variants of unknown clinical significance. The ability to download the fully processed dataset on a per-protein database would be of more interest to researchers focusing on specific proteins or those taking a broader view over multiple proteins (although a facility to download the whole database would be more useful for this final group).

While our website only displays the dataset per protein, the whole dataset, including all the MAVISp entries, is available at our OSF repository (https://osf.io/ufpzm/), which is cited in the paper and linked on the MAVISp website. We have further modified the MAVISp database to add a link to the repository in the modes page, so that it is more visible.

My expertise. - I am a protein bioinformatician with a background in variant effect prediction and large-scale data analysis.

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

Evidence, reproducibility and clarity:

Summary:

The authors present MAVISp, a tool for viewing protein variants heavily based on protein structure information. The authors have done a very impressive amount of curation on various protein targets, and should be commended for their efforts. The tool includes a diverse array of experimental, clinical, and computational data sources that provides value to potential users interested in a given target.

Major comments:

Unfortunately I was not able to get the website to work correctly. When selecting a protein target in simple mode, I was greeted with a completely blank page in the app window. In ensemble mode, there was no transition away from the list of targets at all. I'm using Firefox 140.0.2 (64-bit) on Ubuntu 22.04. I would like to explore the data myself and provide feedback on the user experience and utility.

We have tried reproducing the issue mentioned by the reviewer, using the exact same Ubuntu and Firefox versions, but unfortunately failed to produce it. The website worked fine for us under such an environment. The issue experienced by the reviewer may have been due to either a temporary issue with the web server or a problem with the specific browser environment they were working in, which we are unable to reproduce. It would be useful to know the date that this happened to verify if it was a downtime on the DTU IT services side that made the webserver inaccessible.

I have some serious concerns about the sustainability of the project and think that additional clarifications in the text could help. Currently is there a way to easily update a dataset to add, remove, or update a component (for example, if a new predictor is published, an error is found in a predictor dataset, or a predictor is updated)? If it requires a new round of manual curation for each protein to do this, I am worried that this will not scale and will leave the project with many out of date entries. The diversity of software tools (e.g., three different pipeline frameworks) also seems quite challenging to maintain.

We appreciate the reviewer’s concerns about long-term sustainability. It is a fair point that we consider within our steering group, who oversee and plans the activities and meet monthly. Adding entries to MAVISp is moving more and more towards automation as we grow. We aim to minimize the manual work where applicable. Still, an expert-based intervention is really needed in some of the steps, and we do not want to renounce it. We intend to keep working on MAVISp to make the process of adding and updating entries as automated as possible, and to streamline the process when manual intervention is necessary. From the point of view of the biocurators, they have three core workflows to use for the default modules, which also automatically cover the source of annotations. We are currently working to streamline the procedures behind LOCAL_INTERACTION, which is the most challenging one. On the data manager and maintainers' side, we have workflows and protocols that help us in terms of automation, quality control, etc, and we keep working to improve them. Among these, we have workflows to use for the old entries updates. As an example, the update of erroneously attributed RefSeq data (pointed out by reviewer 2) took us only one week overall (from assigning revisions and importing to the database) because we have a reduced version of Snakemake for automation that can act on only the affected modules. Also, another point is that we have streamlined the generation of the templates for the gitbook reports (see also answer to reviewer 2).

The update of old entries is planned and made regularly. We also deposit the old datasets on OSF for transparency, in case someone needs to navigate and explore the changes. We have activities planned between May and August every year to update the old entries in relation to changes of protocols in the modules, updates in the core databases that we interact with (COSMIC, Clinvar etc). In case of major changes, the activities for updates continue in the Fall. Other revisions can happen outside these time windows if an entry is needed or a specific research project and needs updates too.

Furthermore, the community of people contributing to MAVISp as biocurators or developers is growing and we have scientists contributing from other groups in relation to their research interest. We envision that for this resource to scale up, our team cannot be the only one producing data and depositing it to the database. To facilitate this we launched a pilot for a training event online (see Event page on the website) and we will repeat it once per year. We also organize regular meetings with all the active curators and developers to plan the activities in a sustainable manner and address the challenges we encounter.

As stated in the manuscript, currently with the team of people involved, automatization and resources that we have gathered around this initiative we can provide updates to the public database every third month and we have been regularly satisfied with them. Additionally, we are capable of processing from 20 to 40 proteins every month depending also on the needs of revision or expansion of analyses on existing proteins. We also depend on these data for our own research projects and we are fully committed to it.

Additionally, we are planning future activities in these directions to improve scale up and sustainability:

• Streamlining manual steps so that they are as convenient as fast as possible for our curators, e.g. by providing custom pages on the MAVISp website
• Streamline and automatize the generation of useful output, for instance the reports, by using a combination of simple automation and large language models
• Implement ways to share our software and scripts with third parties, for instance by providing ready made (or close to) containers or virtual machines
• For a future version 2 if the database grows in a direction that is not compatible with Streamlit, the web data science framework we are currently using, we will rewrite the website using a framework that would allow better flexibility and performance, for instance using Django and a proper database backend. On the same theme, according to the GitHub repository, the program relies on Python 3.9, which reaches end of life in October 2025. It has been tested against Ubuntu 18.04, which left standard support in May 2023. The authors should update the software to more modern versions of Python to promote the long-term health and maintainability of the project.

We thank the reviewer for this comment - we are aware of the upcoming EOL of Python 3.9. We tested MAVISp, both software package and web server, using Python 3.10 (which is the minimum supported version going forward) and Python 3.13 (which is the latest stable release at the time of writing) and updated the instructions in the README file on the MAVISp GitHub repository accordingly.

We plan on keeping track of Python and library versions during our testing and updating them when necessary. In the future, we also plan to deploy Continuous Integration with automated testing for our repository, making this process easier and more standardized.

I appreciate that the authors have made their code and data available. These artifacts should also be versioned and archived in a service like Zenodo, so that researchers who rely on or want to refer to specific versions can do so in their own future publications.

Since 2024, we have been reporting all previous versions of the dataset on OSF, the repository linked to the MAVISp website, at https://osf.io/ufpzm/files/osfstorage (folder: previous_releases). We prefer to keep everything under OSF, as we also use it to deposit, for example, the MD trajectory data.

Additionally, in this GitHub page that we use as a space to interact between biocurators, developers, and data managers within the MAVISp community, we also report all the changes in the NEWS space: https://github.com/ELELAB/mavisp_data_collection

Finally, the individual tools are all available in our GitHub repository, where version control is in place (see Table S1, where we now mapped all the resources used in the framework)

In the introduction of the paper, the authors conflate the clinical challenges of variant classification with evidence generation and it's quite muddled together. They should strongly consider splitting the first paragraph into two paragraphs - one about challenges in variant classification/clinical genetics/precision oncology and another about variant effect prediction and experimental methods. The authors should also note that they are many predictors other than AlphaMissense, and may want to cite the ClinGen recommendations (PMID: 36413997) in the intro instead.

We revised the introduction in light of these suggestions. We have split the paragraph as recommended and added a longer second paragraph about VEPs and using structural data in the context of VEPs. We have also added the citation that the reviewer kindly recommended.

Also in the introduction on lines 21-22 the authors assert that "a mechanistic understanding of variant effects is essential knowledge" for a variety of clinical outcomes. While this is nice, it is clearly not the case as we can classify variants according to the ACMG/AMP guidelines without any notion of specific mechanism (for example, by combining population frequency data, in silico predictor data, and functional assay data). The authors should revise the statement so that it's clear that mechanistic understanding is a worthy aspiration rather than a prerequisite.

We revised the statement in light of this comment from the reviewer

In the structural analysis section (page 5, lines 154-155 and elsewhere), the authors define cutoffs with convenient round numbers. Is there a citation for these values or were these arbitrarily chosen by the authors? I would have liked to see some justification that these assignments are reasonable. Also there seems to be an error in the text where values between -2 and -3 kcal/mol are not assigned to a bin (I assume they should also be uncertain). There are other similar seemingly-arbitrary cutoffs later in the section that should also be explained.

We have revised the text making the two intervals explicit, for better clarity.

On page 9, lines 294-298 the authors talk about using the PTEN data from ProteinGym, rather than the actual cutoffs from the paper. They get to the latter later on, but I'm not sure why this isn't first? The ProteinGym cutoffs are somewhat arbitrarily based on the median rather than expert evaluation of the dataset, and I'm not sure why it's even worth mentioning them when proper classifications are available. Regarding PTEN, it would be quite interesting to see a comparison of the VAMP-seq PTEN data and the Mighell phosphatase assay, which is cited on page 9 line 288 but is not actually a VAMP-seq dataset. I think this section could be interesting but it requires some additional attention.

We have included the data from Mighell’s phosphatase assay as provided by MAVEdb in the MAVISp database, within the experimental_data module for PTEN, and we have revised the case study, including them and explaining better the decision of supporting both the ProteinGym and MAVEdb classification in MAVISp (when available). See revised Figure3, Table 1 and corresponding text.

The authors mention "pathogenicity predictors" and otherwise use pathogenicity incorrectly throughout the manuscript. Pathogenicity is a classification for a variant after it has been curated according to a framework like the ACMG/AMP guidelines (Richards 2015 and amendments). A single tool cannot predict or assign pathogenicity - the AlphaMissense paper was wrong to use this nomenclature and these authors should not compound this mistake. These predictors should be referred to as "variant effect predictors" or similar, and they are able to produce evidence towards pathogenicity or benignity but not make pathogenicity calls themselves. For example, in Figure 4e, the terms "pathogenic" and "benign" should only be used here if these are the classifications the authors have derived from ClinVar or a similar source of clinically classified variants.

The reviewer is correct, we have revised the terminology we used in the manuscript and refers to VEPs (Variant Effect Predictors)

Minor comments:

The target selection table on the website needs some kind of text filtering option. It's very tedious to have to find a protein by scrolling through the table rather than typing in the symbol. This will only get worse as more datasets are added.

We have revised the website, adding a filtering option. In detail, we have refactored the web app by adding filtering functionality, both for the main protein table (that can now be filtered by UniProt AC, gene name, or RefSeq ID) and the mutations table. Doing this required a general overhaul of the table infrastructure (we changed the underlying engine that renders the tables).

The data sources listed on the data usage section of the website are not concordant with what is in the paper. For example, MaveDB is not listed.

We have revised and updated the data sources on the website, adding a metadata section with relevant information, including MaveDB references where applicable.

Figure 2 is somewhat confusing, as it partially interleaves results from two different proteins. This would be nicer as two separate figures, one on each protein, or just of a single protein.

As suggested by the reviewer, we have now revised the figure and corresponding legends and text, focusing only on one of the two proteins.

Figure 3 panel b is distractingly large and I wonder if the authors could do a little bit more with this visualization.

We have revised Figure 3 to solve these issues and integrating new data from the comparison with the phosphatase assay

Capitalization is inconsistent throughout the manuscript. For example, page 9 line 288 refers to VampSEQ instead of VAMP-seq (although this is correct elsewhere). MaveDB is referred to as MAVEdb or MAVEDB in various places. AlphaMissense is referred to as Alphamissense in the Figure 5 legend. The authors should make a careful pass through the manuscript to address this kind of issues.

We have carefully proofread the paper for these inconsistencies

MaveDB has a more recent paper (PMID: 39838450) that should be cited instead of/in addition to Esposito et al.

We have added the reference that the reviewer recommended

On page 11, lines 338-339 the authors mention some interesting proteins including BLC2, which has base editor data available (PMID: 35288574). Are there plans to incorporate this type of functional assay data into MAVISp?

The assay mentioned in the paper refers to an experimental setup designed to investigate mutations that may confer resistance to the drug venetoclax. We started the first steps to implement a MAVISp module aimed at evaluating the impact of mutations on drug binding using alchemical free energy perturbations (ensemble mode) but we are far from having it complete. We expect to import these data when the module will be finalized since they can be used to benchmark it and BCL2 is one of the proteins that we are using to develop and test the new module.

Reviewer #3 (Significance (Required)):

Significance:

General assessment:

This is a nice resource and the authors have clearly put a lot of effort in. They should be celebrated for their achievments in curating the diverse datasets, and the GitBooks are a nice approach. However, I wasn't able to get the website to work and I have raised several issues with the paper itself that I think should be addressed.

Advance:

New ways to explore and integrate complex data like protein structures and variant effects are always interesting and welcome. I appreciate the effort towards manual curation of datasets. This work is very similar in theme to existing tools like Genomics 2 Proteins portal (PMID: 38260256) and ProtVar (PMID: 38769064). Unfortunately as I wasn't able to use the site I can't comment further on MAVISp's position in the landscape.

We have expanded the conclusions section to add a comparison and cite previously published work, and linked to a review we published last year that frames MAVISp in the context of computational frameworks for the prediction of variant effects. In brief, the Genomics 2 Proteins portal (G2P) includes data from several sources, including some overlapping with MAVISp such as Phosphosite or MAVEdb, as well as features calculated on the protein structure. ProtVar also aggregates mutations from different sources and includes both variant effect predictors and predictions of changes in stability upon mutation, as well as predictions of complex structures. These approaches are only partially overlapping with MAVISp. G2P is primarily focused on structural and other annotations of the effect of a mutation; it doesn’t include features about changes of stability, binding, or long-range effects, and doesn’t attempt to classify the impact of a mutation according to its measurements. It also doesn’t include information on protein dynamics. Similarly, ProtVar does include information on binding free energies, long effects, or dynamical information.

Audience:

MAVISp could appeal to a diverse group of researchers who are interested in the biology or biochemistry of proteins that are included, or are interested in protein variants in general either from a computational/machine learning perspective or from a genetics/genomics perspective.

My expertise:

I am an expert in high-throughput functional genomics experiments and am an experienced computational biologist with software engineering experience.

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

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

Summary:

The authors present MAVISp, a tool for viewing protein variants heavily based on protein structure information. The authors have done a very impressive amount of curation on various protein targets, and should be commended for their efforts. The tool includes a diverse array of experimental, clinical, and computational data sources that provides value to potential users interested in a given target.

Major comments:

Unfortunately I was not able to get the website to work properly. When selecting a protein target in simple mode, I was greeted with a completely blank page in the app window, and in ensemble mode, there was no transition away from the list of targets at all. I'm using Firefox 140.0.2 (64-bit) on Ubuntu 22.04. I would have liked to be able to explore the data myself and provide feedback on the user experience and utility.

I have some serious concerns about the sustainability of the project and think that additional clarifications in the text could help. Currently is there a way to easily update a dataset to add, remove, or update a component (for example, if a new predictor is published, an error is found in a predictor dataset, or a predictor is updated)? If it requires a new round of manual curation for each protein to do this, I am worried that this will not scale and will leave the project with many out of date entries. The diversity of software tools (e.g., three different pipeline frameworks) also seems quite challenging to maintain.

On the same theme, according to the GitHub repository, the program relies on Python 3.9, which reaches end of life in October 2025. It has been tested against Ubuntu 18.04, which left standard support in May 2023. The authors should update the software to more modern versions of Python to promote the long-term health and maintainability of the project.

I appreciate that the authors have made their code and data available. These artifacts should also be versioned and archived in a service like Zenodo, so that researchers who rely on or want to refer to specific versions can do so in their own future publications.

In the introduction of the paper, the authors conflate the clinical challenges of variant classification with evidence generation and it's quite muddled together. The y should strongly consider splitting the first paragraph into two paragraphs - one about challenges in variant classification/clinical genetics/precision oncology and another about variant effect prediction and experimental methods. The authors should also note that they are many predictors other than AlphaMissense, and may want to cite the ClinGen recommendations (PMID: 36413997) in the intro instead.

Also in the introduction on lines 21-22 the authors assert that "a mechanistic understanding of variant effects is essential knowledge" for a variety of clinical outcomes. While this is nice, it is clearly not the case as we are able to classify variants according to the ACMG/AMP guidelines without any notion of specific mechanism (for example, by combining population frequency data, in silico predictor data, and functional assay data). The authors should revise the statement so that it's clear that mechanistic understanding is a worthy aspiration rather than a prerequisite.

In the structural analysis section (page 5, lines 154-155 and elsewhere), the authors define cutoffs with convenient round numbers. Is there a citation for these values or were these arbitrarily chosen by the authors? I would have liked to see some justification that these assignments are reasonable. Also there seems to be an error in the text where values between -2 and -3 kcal/mol are not assigned to a bin (I assume they should also be uncertain). There are other similar seemingly-arbitrary cutoffs later in the section that should also be explained.

On page 9, lines 294-298 the authors talk about using the PTEN data from ProteinGym, rather than the actual cutoffs from the paper. They get to the latter later on, but I'm not sure why this isn't first? The ProteinGym cutoffs are somewhat arbitrarily based on the median rather than expert evaluation of the dataset and I'm not sure why it's even worth mentioning them when proper classifications are available. Regarding PTEN, it would be quite interesting to see a comparison of the VAMP-seq PTEN data and the Mighell phosphatase assay, which is cited on page 9 line 288 but is not actually a VAMP-seq dataset. I think this section could be interesting but it requires some additional attention.

The authors mention "pathogenicity predictors" and otherwise use pathogenicity incorrectly throughout the manuscript. Pathogenicity is a classification for a variant after it has been curated according to a framework like the ACMG/AMP guidelines (Richards 2015 and amendments). A single tool cannot predict or assign pathogenicity - the AlphaMissense paper was wrong to use this nomenclature and these authors should not compound this mistake. These predictors should be referred to as "variant effect predictors" or similar, and they are able to produce evidence towards pathogenicity or benignity but not make pathogenicity calls themselves. For example, in Figure 4e, the terms "pathogenic" and "benign" should only be used here if these are the classifications the authors have derived from ClinVar or a similar source of clinically classified variants.

Minor comments:

The target selection table on the website needs some kind of text filtering option. It's very tedious to have to find a protein by scrolling through the table rather than typing in the symbol. This will only get worse as more datasets are added.

The data sources listed on the data usage section of the website are not concordant with what is in the paper. For example, MaveDB is not listed.

I found Figure 2 to be a bit confusing in that it partially interleaves results from two different proteins. I think this would be nicer as two separate figures, one on each protein, or just of a single protein.

Figure 3 panel b is distractingly large and I wonder if the authors could do a little bit more with this visualization.

Capitalization is inconsistent throughout the manuscript. For example, page 9 line 288 refers to VampSEQ instead of VAMP-seq (although this is correct elsewhere). MaveDB is referred to as MAVEdb or MAVEDB in various places. AlphaMissense is referred to as Alphamissense in the Figure 5 legend. The authors should make a careful pass through the manuscript to address this kind of issues.

MaveDB has a more recent paper (PMID: 39838450) that should be cited instead of/in addition to Esposito et al.

On page 11, lines 338-339 the authors mention some interesting proteins including BLC2, which has base editor data available (PMID: 35288574). Are there plans to incorporate this type of functional assay data into MAVISp?

Significance

General assessment:

This is a nice resource and the authors have clearly put a lot of effort in. They should be celebrated for their achievments in curating the diverse datasets, and the GitBooks are a nice approach. However, I wasn't able to get the website to work and I have raised several issues with the paper itself that I think should be addressed.

Advance:

New ways to explore and integrate complex data like protein structures and variant effects are always interesting and welcome. I appreciate the effort towards manual curation of datasets. This work is very similar in theme to existing tools like Genomics 2 Proteins portal (PMID: 38260256) and ProtVar (PMID: 38769064). Unfortunately as I wasn't able to use the site I can't comment further on MAVISp's position in the landscape.

Audience:

MAVISp could appeal to a diverse group of researchers who are interested in the biology or biochemistry of proteins that are included, or are interested in protein variants in general either from a computational/machine learning perspective or from a genetics/genomics perspective.

My expertise:

I am an expert in high-throughput functional genomics experiments and am an experienced computational biologist with software engineering experience.

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

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary:

The authors present a pipeline and platform, MAVISp, for aggregating, displaying and analysis of variant effects with a focus on reclassification of variants of uncertain clinical significance and uncovering the molecular mechanisms underlying the mutations.

Major comments:

• On testing the platform, I was unable to look-up a specific variant in ADCK1 (rs200211943, R115Q). I found that despite stating that the mapped refseq ID was NP_001136017 in the HGVSp column, it was actually mapped to the canonical UniProt sequence (Q86TW2-1). NP_001136017 actually maps to Q86TW2-3, which is missing residues 74-148 compared to the -1 isoform. The Uniprot canonical sequence has no exact RefSeq mapping, so the HGVSp column is incorrect in this instance. This mapping issue may also affect other proteins and result in incorrect HGVSp identifiers for variants.
• The paper lacks a section on how to properly interpret the results of the MAVISp platform (the case-studies are useful, but don't lay down any global rules for interpreting the results). For example: How should a variant with conflicts between the variant impact predictors be interpreted? Are certain indicators considered more 'reliable' than others?
• In the Methods section, GEMME is stated as being rank-normalised with 0.5 as a threshold for damaging variants. On checking the data downloaded from the site, GEMME was not rank-normalised but rather min-max normalised. Furthermore, Supplementary text S4 conflicts with the methods section over how GEMME scores are classified, S4 states that a raw-value threshold of -3 is used.
• Note. This is a major comment as one of the claims is that the associated web-tool is user-friendly. While functional, the web app is very awkward to use for analysis on any more than a few variants at once.
  • The fixed window size of the protein table necessitates excessive scrolling to reach your protein-of-interest. This will also get worse as more proteins are added. Suggestion: add a search/filter bar.
  • The same applies to the dataset window.
  • You are unable to copy anything out of the tables.
  • Hyperlinks in the tables only seem to work if you open them in a new tab or window.
  • All entries in the reference column point to the MAVISp preprint even when data from other sources is displayed (e.g. MAVE studies).
  • Entering multiple mutants in the "mutations to be displayed" window is time-consuming for more than a handful of mutants. Suggestion: Add a box where multiple mutants can be pasted in at once from an external document.

Minor comments

• Grammar. I appreciate that this manuscript may have been compiled by a non-native English speaker, but I would be remiss not to point out that there are numerous grammar errors throughout, usually sentence order issues or non-pluralisation. The meaning of the authors is mostly clear, but I recommend very thoroughly proof-reading the final version.
• There are numerous proteins that I know have high-quality MAVE datasets that are absent in the database e.g. BRCA1, HRAS and PPARG.
• Checking one of the existing MAVE datasets (KRAS), I found that the variants were annotated as damaging, neutral or given a positive score (these appear to stand-in for gain-of-function variants). For better correspondence with the other columns, those with positive scores could be labelled as 'ambiguous' or 'uncertain'.
• Numerous thresholds are defined for stabilizing / destabilizing / neutral variants in both the STABILITY and the LOCAL_INTERACTION modules. How were these thresholds determined? I note that (PMC9795540) uses a ΔΔG threshold of 1/-1 for defining stabilizing and destabilizing variants, which is relatively standard (though they also say that 2-3 would likely be better for pinpointing pathogenic variants).
• "Overall, with the examples in this section, we illustrate different applications of the MAVISp results, spanning from benchmarking purposes, using the experimental data to link predicted functional effects with structural mechanisms or using experimental data to validate the predictions from the MAVISp modules."

The last of these points is not an application of MAVISp, but rather a way in which external data can help validate MAVISp results. Furthermore, none of the examples given demonstrate an application in benchmarking (what is being benchmarked?). - Transcription factors section. This section describes an intended future expansion to MAVISp, not a current feature, and presents no results. As such, it should probably be moved to the conclusions/future directions section. - Figures. The dot-plots generated by the web app, and in Figures 4, 5 and 6 have 2 legends. After looking at a few, it is clear that the lower legend refers to the colour of the variant on the X-axis - most likely referencing the ClinVar effect category. This is not, however, made clear either on the figures or in the app. - "We identified ten variants reported in ClinVar as VUS (E102K, H86D, T29I, V91I, P2R, L44P, L44F, D56G, R11L, and E25Q, Fig.5a)"

E25Q is benign in ClinVar and has had that status since first submitted.

Significance

Platforms that aggregate predictors of variant effect are not a new concept, for example dbNSFP is a database of SNV predictions from variant effect predictors and conservation predictors over the whole human proteome. Predictors such as CADD and PolyPhen-2 will often provide a summary of other predictions (their features) when using their platforms. MAVISp's unique angle on the problem is in the inclusion of diverse predictors from each of its different moules, giving a much wider perspective on variants and potentially allowing the user to identify the mechanistic cause of pathogenicity. The visualisation aspect of the web app is also a useful addition, although the user interface is somewhat awkward. Potentially the most valuable aspect of this study is the associated gitbook resource containing reports from biocurators for proteins that link relevant literature and analyse ClinVar variants. Unfortunately, these are only currently available for a small minority of the total proteins in the database with such reports.

For improvement, I think that the paper should focus more on the precise utility of the web app / gitbook reports and how to interpret the results rather than going into detail about the underlying pipeline.

In terms of audience, the fast look-up and visualisation aspects of the web-platform are likely to be of interest to clinicians in the interpretation of variants of unknown clinical significance. The ability to download the fully processed dataset on a per-protein database would be of more interest to researchers focusing on specific proteins or those taking a broader view over multiple proteins (although a facility to download the whole database would be more useful for this final group).

My expertise.

• I am a protein bioinformatician with a background in variant effect prediction and large-scale data analysis.

Author response:

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

Reviewer #1 (Public review):

Summary:

Syed et al. investigate the circuit underpinnings for leg grooming in the fruit fly. They identify two populations of local interneurons in the right front leg neuromere of ventral nerve cord, i.e. 62 13A neurons and 64 13B neurons. Hierarchical clustering analysis identifies 10 morphological classes for both populations. Connectome analysis reveals their circuit interactions: these GABAergic interneurons provide synaptic inhibition either between the two subpopulations, i.e., 13B onto 13A, or among each other, i.e., 13As onto other 13As, and/or onto leg motoneurons, i.e., 13As and 13Bs onto leg motoneurons. Interestingly, 13A interneurons fall into two categories, with one providing inhibition onto a broad group of motoneurons, being called "generalists", while others project to a few motoneurons only, being called "specialists". Optogenetic activation and silencing of both subsets strongly affect leg grooming. As well aas ctivating or silencing subpopulations, i.e., 3 to 6 elements of the 13A and 13B groups, has marked effects on leg grooming, including frequency and joint positions, and even interrupting leg grooming. The authors present a computational model with the four circuit motifs found, i.e., feed-forward inhibition, disinhibition, reciprocal inhibition, and redundant inhibition. This model can reproduce relevant aspects of the grooming behavior.

Strengths:

The authors succeeded in providing evidence for neural circuits interacting by means of synaptic inhibition to play an important role in the generation of a fast rhythmic insect motor behavior, i.e., grooming. Two populations of local interneurons in the fruit fly VNC comprise four inhibitory circuit motifs of neural action and interaction: feed-forward inhibition, disinhibition, reciprocal inhibition, and redundant inhibition. Connectome analysis identifies the similarities and differences between individual members of the two interneuron populations. Modulating the activity of small subsets of these interneuron populations markedly affects the generation of the motor behavior, thereby exemplifying their important role in generating grooming.

We thank the reviewer for their thoughtful and constructive evaluation of our work. 

Weaknesses:

Effects of modulating activity in the interneuron populations by means of optogenetics were conducted in the so-called closed-loop condition. This does not allow for differentiation between direct and secondary effects of the experimental modification in neural activity, as feedforward and feedback effects cannot be disentangled. To do so, open loop experiments, e.g., in deafferented conditions, would be important. Given that many members of the two populations of interneurons do not show one, but two or more circuit motifs, it remains to be disentangled which role the individual circuit motif plays in the generation of the motor behavior in intact animals.

Our optogenetic experiments show a role for 13A/B neurons in grooming leg movements – in an intact sensorimotor system - but we cannot yet differentiate between central and reafferent contributions. Activation of 13As or 13Bs disinhibits motor neurons and that is sufficient to induce walking/grooming. Therefore, we can show a role for the disinhibition motif.

Proprioceptive feedback from leg movements could certainly affect the function of these reciprocal inhibition circuits. Given the synapses we observe between leg proprioceptors and 13A neurons, we think this is likely.

Our previous work (Ravbar et al 2021) showed that grooming rhythms in dusted flies persist when sensory feedback is reduced, indicating that central control is possible. In those experiments, we used dust to stimulate grooming and optogenetic manipulation to broadly silence sensory feedback. We cannot do the same here because we do not yet have reagents to separately activate sparse subsets of inhibitory neurons while silencing specific proprioceptive neurons. More importantly, globally silencing proprioceptors would produce pleiotropic effects and severely impair baseline coordination, making it difficult to distinguish whether observed changes reflect disrupted rhythm generation or secondary consequences of impaired sensory input. Therefore, the reviewer is correct – we do not know whether the effects we observe are feedforward (central), feedback sensory, or both. We have included this in the revised results and discussion section to describe these possibilities and the limits of our current findings.

Additionally, we have used a computational model to test the role of each motif separately and we show that in the results.

Reviewer #2 (Public review):

Summary:

This manuscript by Syed et al. presents a detailed investigation of inhibitory interneurons, specifically from the 13A and 13B hemilineages, which contribute to the generation of rhythmic leg movements underlying grooming behavior in Drosophila. After performing a detailed connectomic analysis, which offers novel insights into the organization of premotor inhibitory circuits, the authors build on this anatomical framework by performing optogenetic perturbation experiments to functionally test predictions derived from the connectome. Finally, they integrate these findings into a computational model that links anatomical connectivity with behavior, offering a systems-level view of how inhibitory circuits may contribute to grooming pattern generation.

Strengths:

(1) Performing an extensive and detailed connectomic analysis, which offers novel insights into the organization of premotor inhibitory circuits.

(2) Making sense of the largely uncharacterized 13A/13B nerve cord circuitry by combining connectomics and optogenetics is very impressive and will lay the foundation for future experiments in this field.

(3) Testing the predictions from experiments using a simplified and elegant model.

We thank the reviewer for their thoughtful and encouraging evaluation of our work. 

Weaknesses:

(1) In Figure 4, while the authors report statistically significant shifts in both proximal inter-leg distance and movement frequency across conditions, the distributions largely overlap, and only in Panel K (13B silencing) is there a noticeable deviation from the expected 7-8 Hz grooming frequency. Could the authors clarify whether these changes truly reflect disruption of the grooming rhythm? 

We reanalyzed the dataset with Linear Mixed Models. We find significant differences in mean frequencies upon silencing these neurons but not upon activation. The experimental groups are also significantly more variable. We revised these panels with updated analysis. We think these data do support our interpretation that the grooming rhythms are disrupted. 

More importantly, all this data would make the most sense if it were performed in undusted flies (with controls) as is done in the next figure.

In our assay conditions, undusted flies groom infrequently. We used undusted flies for some optogenetic activation experiments, where the neuron activation triggers behavior initiation, but we chose to analyze the effect of silencing inhibitory neurons in dusted flies because dust reliably activates mechanosensory neurons and elicits robust grooming behavior enabling us to assess how manipulation of 13A/B neurons alters grooming rhythmicity and leg coordination.

(2) In Figure 4-Figure Supplement 1, the inclusion of walking assays in dusted flies is problematic, as these flies are already strongly biased toward grooming behavior and rarely walk. To assess how 13A neuron activation influences walking, such experiments should be conducted in undusted flies under baseline locomotor conditions.

We agree that there are better ways to assay potential contributions of 13A/13B neurons to walking. We intended to focus on how normal activity in these inhibitory neurons affects coordination during grooming, and we included walking because we observed it in our optogenetic experiments and because it also involves rhythmic leg movements. The walking data is reported in a supplementary figure because we think this merits further study with assays designed to quantify walking specifically. We will make these goals clearer in the revised manuscript and we are happy to share our reagents with other research groups more equipped to analyze walking differences.

(3) For broader lines targeting six or more 13A neurons, the authors provide specific predictions about expected behavioral effects-e.g., that activation should bias the limb toward flexion and silencing should bias toward extension based on connectivity to motor neurons. Yet, when using the more restricted line labeling only two 13A neurons (Figure 4 - Figure Supplement 2), no such prediction is made. The authors report disrupted grooming but do not specify whether the disruption is expected to bias the movement toward flexion or extension, nor do they discuss the muscle target. This is a missed opportunity to apply the same level of mechanistic reasoning that was used for broader manipulations.

Because we cannot unambiguously identify one of the neurons from our sparsest 13A splitGAL4 lines in FANC, we cannot say with certainty which motor neurons they target. That limits the accuracy of any functional predictions.  

(4) Regarding Figure 5: The 70ms on/off stimulation with a slow opsin seems problematic. CsChrimson off kinetics are slow and unlikely to cause actual activity changes in the desired neurons with the temporal precision the authors are suggesting they get. Regardless, it is amazing that the authors get the behavior! It would still be important for the authors to mention the optogenetics caveat, and potentially supplement the data with stimulation at different frequencies, or using faster opsins like ChrimsonR.

We were also intrigued by the behavioral consequences of activating these inhibitory neurons with CsChrimson. We appreciate the reviewer’s point that CsChrimson’s slow off-kinetics limit precise temporal control. To address this, we repeated our frequency analysis using a range of pulse durations (10/10, 50/50, 70/70, 110/110, and 120/120 ms on/off) and compared the mean frequency of proximal joint extension/flexion cycles across conditions. We found no significant difference in frequency (LLMS, p > 0.05), suggesting that the observed grooming rhythm is not dictated by pulse period but instead reflects an intrinsic property of the premotor circuit once activated. We now include these results in ‘Figure 5—figure supplement 1’ and clarify in the text that we interpret pulsed activation as triggering, rather than precisely pacing, the endogenous grooming rhythm. We continue to note in the manuscript that CsChrimson’s slow off-kinetics may limit temporal precision. We will try ChrimsonR in future experiments.

Overall, I think the strengths outweigh the weaknesses, and I consider this a timely and comprehensive addition to the field.

Reviewer #3 (Public review):

Summary:

The authors set out to determine how GABAergic inhibitory premotor circuits contribute to the rhythmic alternation of leg flexion and extension during Drosophila grooming. To do this, they first mapped the ~120 13A and 13B hemilineage inhibitory neurons in the prothoracic segment of the VNC and clustered them by morphology and synaptic partners. They then tested the contribution of these cells to flexion and extension using optogenetic activation and inhibition and kinematic analyses of limb joints. Finally, they produced a computational model representing an abstract version of the circuit to determine how the connectivity identified in EM might relate to functional output. The study, in its current form, makes an important but overclaimed contribution to the literature due to a mismatch between the claims in the paper and the data presented.

Strengths:

The authors have identified an interesting question and use a strong set of complementary tools to address it:

(1) They analysed serial‐section TEM data to obtain reconstructions of every 13A and 13B neuron in the prothoracic segment. They manually proofread over 60 13A neurons and 64 13B neurons, then used automated synapse detection to build detailed connectivity maps and cluster neurons into functional motifs.

(2) They used optogenetic tools with a range of genetic driver lines in freely behaving flies to test the contribution of subsets of 13A and 13B neurons.

(3) They used a connectome-constrained computational model to determine how the mapped connectivity relates to the rhythmic output of the behavior.

Weaknesses:

The manuscript aims to reveal an instructive, rhythm-generating role for premotor inhibition in coordinating the multi-joint leg synergies underlying grooming. It makes a valuable contribution, but currently, the main claims in the paper are not well-supported by the presented evidence.

Major points

(1) Starting with the title of this manuscript, "Inhibitory circuits generate rhythms for leg movements during Drosophila grooming", the authors raise the expectation that they will show that the 13A and 13B hemilineages produce rhythmic output that underlies grooming. This manuscript does not show that. For instance, to test how they drive the rhythmic leg movements that underlie grooming requires the authors to test whether these neurons produce the rhythmic output underlying behavior in the absence of rhythmic input. Because the optogenetic pulses used for stimulation were rhythmic, the authors cannot make this point, and the modelling uses a "black box" excitatory network, the output of which might be rhythmic (this is not shown). Therefore, the evidence (behavioral entrainment; perturbation effects; computational model) is all indirect, meaning that the paper's claim that "inhibitory circuits generate rhythms" rests on inferred sufficiency. A direct recording (e.g., calcium imaging or patch-clamp) from 13A/13B during grooming - outside the scope of the study - would be needed to show intrinsic rhythmogenesis. The conclusions drawn from the data should therefore be tempered. Moreover, the "black box" needs to be opened. What output does it produce? How exactly is it connected to the 13A-13B circuit? 

We modified the title to better reflect our strongest conclusions: “Inhibitory circuits control leg movements during Drosophila grooming”

Our optogenetic activation was delivered in a patterned (70 ms on/off) fashion that entrains rhythmic movements, but this does not rule out the possibility that the rhythm is imposed externally. In the manuscript, we state that we used pulsed light to mimic a flexion-extension cycle and note that this approach tests whether inhibition is sufficient to drive rhythmic leg movements when temporally patterned. While this does not prove that 13A/13B neurons are intrinsic rhythm generators, it does demonstrate that activating subsets of inhibitory neurons is sufficient to elicit alternating leg movements resembling natural grooming and walking.

Our goal with the model was to demonstrate that it is possible to produce rhythmic outputs with this 13A/B circuit, based on the connectome. The “black box” is a small recurrent neural network (RNN) consisting of 40 neurons in its hidden layer. The inputs are the “dust” levels from the environment (the green pixels in Figure 6I), the “proprioceptive” inputs (“efference copy” from motor neurons), and the amount of dust accumulated on both legs. The outputs (all positive) connect to the 13A neurons, the 13B neurons, and to the motor neurons. We refer to it as the “black box” because we make no claims about the actual excitatory inputs to these circuits. Its function is to provide input, needed to run the network, that reflects the distribution of “dust” in the environment as well as the information about the position of the legs.  

The output of the “black box” component of the model might be rhythmic. In fact, in most instances of the model implementation this is indeed the case. However, as mentioned in the current version of the manuscript: “But the 13A circuitry can still produce rhythmic behavior even without those external inputs (or when set to a constant value), although the legs become less coordinated.” Indeed, when we refine the model (with the evolutionary training) without the “black box” (using a constant input of 0.1) the behavior is still rhythmic and sustained. Therefore, the rhythmic activity and behavior can emerge from the premotor circuitry itself without a rhythmic input.

The context in which the 13A and 13B hemilineages sit also needs to be explained. What do we know about the other inputs to the motorneurons studied? What excitatory circuits are there? 

We agree that there are many more excitatory and inhibitory, direct and indirect, connections to motor neurons that will also affect leg movements for grooming and walking. 13A neurons provide a substantial fraction of premotor input. For example, 13As account for ~17.1% of upstream synapses for one tibia extensor (femur seti) motor neuron and ~14.6% for another tibia extensor (femur feti) motor neuron. Our goal was to demonstrate what is possible from a constrained circuit of inhibitory neurons that we mapped in detail, and we hope to add additional components to better replicate the biological circuit as behavioral and biomechanical data is obtained by us and others.  

Furthermore, the introduction ignores many decades of work in other species on the role of inhibitory cell types in motor systems. There is some mention of this in the discussion, but even previous work in Drosophila larvae is not mentioned, nor crustacean STG, nor any other cell types previously studied. This manuscript makes a valuable contribution, but it is not the first to study inhibition in motor systems, and this should be made clear to the reader.

We thank the reviewer for this important reminder.  Previous work on the contribution of inhibitory neurons to invertebrate motor control certainly influenced our research. We have expanded coverage of the relevant history and context in our revised discussion.

(2) The experimental evidence is not always presented convincingly, at times lacking data, quantification, explanation, appropriate rationales, or sufficient interpretation.

We are committed to improving the clarity, rationale, and completeness of our experimental descriptions.  We have revisited the statistical tests applied throughout the manuscript and expanded the Methods.

(3) The statistics used are unlike any I remember having seen, essentially one big t-test followed by correction for multiple comparisons. I wonder whether this approach is optimal for these nested, high‐dimensional behavioral data. For instance, the authors do not report any formal test of normality. This might be an issue given the often skewed distributions of kinematic variables that are reported. Moreover, each fly contributes many video segments, and each segment results in multiple measurements. By treating every segment as an independent observation, the non‐independence of measurements within the same animal is ignored. I think a linear mixed‐effects model (LMM) or generalized linear mixed model (GLMM) might be more appropriate.

We thank the reviewer for raising this important point regarding the statistical treatment of our segmented behavioral data. Our initial analysis used independent t-tests with Bonferroni correction across behavioral classes and features, which allowed us to identify broad effects. However, we acknowledge that this approach does not account for the nested structure of the data. To address this, we re-analyzed key comparisons using linear mixed-effects models (LMMs) as suggested by the reviewer. This approach allowed us to more appropriately model within-fly variability and test the robustness of our conclusions. We have updated the manuscript based on the outcomes of these analyses.

(4) The manuscript mentions that legs are used for walking as well as grooming. While this is welcome, the authors then do not discuss the implications of this in sufficient detail. For instance, how should we interpret that pulsed stimulation of a subset of 13A neurons produces grooming and walking behaviours? How does neural control of grooming interact with that of walking?

We do not know how the inhibitory neurons we investigated will affect walking or how circuits for control of grooming and walking might compete. We speculate that overlapping pre-motor circuits may participate because both have similar extension flexion cycles at similar frequencies, but we do not have hard experimental data to support. This would be an interesting area for future research. Here, we focused on the consequences of activating specific 13A/B neurons during grooming because they were identified through a behavioral screen for grooming disruptions, and we had developed high-resolution assays and familiarity with the normal movements in this behavior.

(5) The manuscript needs to be proofread and edited as there are inconsistencies in labelling in figures, phrasing errors, missing citations of figures in the text, or citations that are not in the correct order, and referencing errors (examples: 81 and 83 are identical; 94 is missing in text).

We have proofread the manuscript to fix figure labeling, citation order, and referencing errors.

Reviewing Editor Comments:

In addition to the recommendations listed below, a common suggestion, given the lack of evidence to support that 13A and 13B are rhythm-generating, is to tone down the title to something like, for example, "Inhibitory circuits control leg movements during grooming in Drosophila" (or similar).

We changed the title to Inhibitory circuits control leg movements during Drosophila  grooming

Reviewer #1 (Recommendations for the authors):

(1) Naming of movements of leg segments:

The authors refer to movements of leg segments across the leg, i.e., of all joints, as "flexion" and "extension". For example, in Figure 4A and at many other places. This naming is functionally misleading for two reasons: (i) the anatomical organization of an insect leg differs in principle from the organization of the mammalian leg, which the manuscript often refers to. While the organization of a mammalian limb is planar the organization of the insect limb shows a different plane as compared to the body length axis (for detailed accounts see Ritzmann et al. 2004; Büschges & Ache, 2024); (ii) the reader cannot differentiate between places in the text, where "flexion" and "extension" refer to movements of the tibia of the femur-tibia joint, e.g. in the graphical abstract, in Figure 3 and its supplements, and other places, e.g. Figure 4 and its supplements, where these two words refer to movements of leg segments of other joints, e.g. thorax-coxa, coxa-trochanter and tarsal joints. The reviewer strongly suggests naming the movements of the leg segments according to the individual joint and its muscles.

We accept this helpful suggestion. We now include a description of the leg segments and joints in the revised Introduction and refer to which leg segments we mean   

“The adult Drosophila leg consists of serially arranged joints—bodywall/thoraco-coxal (Th-C), coxa–trochanter (C-Tr), trochanter–femur (Tr-F), femur–tibia (F-Ti), tibia–tarsus (Ti-Ta)—each powered by opposing flexor and extensor muscles that transmit force through tendons (Soler et al., 2004). The proximal joints, Th-C and C-Tr, mediate leg protraction–retraction and elevation–depression, respectively (Ritzmann et al., 2004; Büschges & Ache, 2025). The medial joint, F-Ti, acts as the principal flexion–extension hinge and is controlled by large tibia extensor motor neurons and flexor motor neurons (Soler et al., 2004; Baek and Mann 2009; Brierley et al., 2012; Azevedo et al., 2024; Lesser et al., 2024). By contrast, distal joints such as Ti-Ta and the tarsomeres contribute to fine adjustments, grasping, and substrate attachment (Azevedo et al., 2024).”

We also clarified femur-tibia joints in the graphical abstract, modified Figure 3 legend and added joints at relevant places.

(2)  Figures 3, 4, and 5 with supplements:

The authors optogenetically silence and activate (sub)populations of 13A and 13B interneurons. Changes in frequency of movements and distance between legs or leg movements are interpreted as the effect of these experimental paradigms. No physiological recordings from leg motoneurons or leg muscles are shown. While I understand the notion of the authors to interpret a movement as the outcome of activity in a muscle, it needs to be remembered that it is well known that fast cyclic leg movements, including those for grooming, cannot be used to conclude on the underlying neural activity. Zakotnik et al. (2006) and others provided evidence that such fast cyclic movements can result from the interaction of the rhythmic activity of one leg muscle only, together with the resting tension of its silent antagonist. Given that no physiological recordings are presented, this needs to be mentioned in the discussion, e.g., in the section "Inhibitory Innervation Imbalance.......".

Added studies from Heitler, 1974; Bennet-Clark, 1975; Zakotnik et al., 2006; Page et al., 2008 in discussion.

(3) Introduction and Discussion:

The authors refer extensively to work on the mammalian spinal cord and compare their own work with circuit elements found in the spinal cord. From the perspective of the reviewer this notion is in conflict with acknowledging prior research work on the role of inhibitory network interactions for other invertebrates and lower vertebrates: such are locust flight system (for feedforward inhibition, disinhibition), crustacean stomatogastric nervous system (reciprocal inhibition), clione swimming system (reciprocal inhibition, feedforward inhibition, disinhibition), leech swimming system (reciprocal inhibition, disinhibition, feedforward inhibition), xenopus swimming system (reciprocal inhibition). The next paragraph illustrates this criticism/suggestion for stick insect neural circuits for leg stepping.

(4) Discussion:

"Feedforward inhibition" and "Disinhibition": it is already been described that rhythmic activity of antagonistic insect leg motoneuron pools arises from alternating synaptic inhibition and disinhibition of the motoneurons from premotor central pattern generating networks, e.g., Büschges (1998); Büschges et al. (2004); Ruthe et al. (2024).

We have added these references to the revised Discussion.

(5) Circuit motifs of the simulation, i.e., mutual inhibition between interneurons and onto motoneurons and sensory feedback influences and pathways share similarities to those formerly used by studies simulating rhythmic insect leg movements, for example, Schilling & Cruse 2020, 2023 or Toth et al. 2012. For the reader, it appears relevant that the progress of the new simulation is explained in the light of similarities and differences to these former approaches with respect to the common circuit motifs used.

We now put our work in the context of other models in the Discussion section: “Similar circuit motifs, namely reciprocal inhibitions between pre-motor neurons and the sensory feedback have been modeled before, in particular neuroWalknet, and such simple motifs do not require a separate CPG component to generate rhythmic behavior in these models (Schilling & Cruse 2020, 2023). However, our model is much simpler than the neuroWalknet - it controls a 2D agent operating on an abstract environment (the dust distribution), without physics. In real animals or complex mechanical models such as NeuroMechFly (Lobato-Rios et al), a more explicit central rhythm generation may be advantageous for the coordination across many more degrees of freedom.”

Reviewer #2 (Recommendations for the authors):

I might have missed this, but I couldn't find any mention of how the grooming command pathways, described by previous work from the authors' lab, recruit these predicted grooming pattern-generating neurons. This should be mentioned in the connectome analysis and also discussed later in the discussion.

13A neurons are direct downstream targets of previously described grooming command neurons. Specifically, the antennal grooming command neuron aDN (Hampel et al., 2015) synapses onto two primary 13As (γ and α; 13As-i) that connect to proximal extensor and medial flexor motor neurons, as well as four other 13As (9a, 9c, 9i, 6e) projecting to body wall extensor motor neurons. The 13As-i also form reciprocal connections with 13As-ii, providing a potential substrate for oscillatory leg movements. aDN connects to homologous 13As on both sides, consistent with the bilateral coordination needed for antennal sweeping. 

The head grooming/leg rubbing command neuron DNg12 (Guo et al., 2022)  synapses directly onto ~50 13As, predominantly those connected to proximal motor neurons. 

While sometimes the structural connectivity suggests pathways for generating rhythmic movements, the extensive interconnections among command neurons and premotor circuits indicate that multiple motifs could contribute to the observed behaviors. Further work will be needed to determine how these inputs are dynamically engaged during normal grooming sequences. We have now added it to the discussion.

I encourage the authors to be explicit about caveats wherever possible: e.g., ectopic expression in genetic tools, potential for other unexplored neurons as rhythm generators (rather than 13A/B), given that the authors never get complete silencing phenotypes, CsChrimson kinetics, neurotransmitter predictions, etc.

We now explain these caveats as follows: Ectopic expression is noted in Figure 1—figure supplement 1, and we added the following to the Discussion: “While our experiments with multiple genetic lines labeling 13A/B neurons consistently implicate these cells in leg coordination, ectopic expression in some lines raises the possibility that other neurons may also contribute to this phenotype. In addition, other excitatory and inhibitory neural circuits, not yet identified, may also contribute to the generation of rhythmic leg movements. Future studies should identify such neurons that regulate rhythmic timing and their interactions with inhibitory circuits.”

We also added a caveat regarding CsChrimson kinetics in the Results. Finally, our identification of these neurons as inhibitory is based on genetic access to the GABAergic population (we use GAD-spGAL4 as part of the intersection which targets them), rather than on predictions of neurotransmitter identity.

Reviewer #3 (Recommendations for the authors):

Detailed list of figure alterations:

(1) Figure 1:

(a) Figure 1B and Figure 1 - Figure Supplement 1 lack information on individual cells - how can we tell that the cells targeted are indeed 13A and 13B, and which ones they are? Since off-target expression in neighboring hemilineages isn't ruled out, the interpretation of results is not straightforward.

The neurons labeled by R35G04-DBD and GAD1-AD are identified as 13A and 13B based on their stereotyped cell body positions and characteristic neurite projections into the neuropil, which match those of 13A and 13B neurons reconstructed in the FANC and MANC connectome. While we have not generated flip-out clones in this genotype, we do isolate 13A neurons more specifically later in the manuscript using R35G04-DBD intersected with Dbx-AD, and show single-cell morphology consistent with identified 13A neurons. The purpose of including this early figure was to motivate the study by showing that silencing this population, which includes 13A/13B neurons, strongly reduces grooming in dusted flies. 

Regarding Figure 1—Figure Supplement 1:

This figure showed the expression patterns of all lines used throughout the manuscript. Panels C and D illustrated lines with minimal to no ectopic expression. Panels A and B show neurons with posterior cell bodies that may correspond to 13A neurons not reconstructed in our dataset but described in Soffers et al., 2025 and Marin et al., 2025 and we have provided detailed information about all VNC expressions in the figure legend.

(b) Figure 1D lacks explanation of boxplots, asterisks, genotypes/experimental design.

Added.

(c) Figures 1E-F and video 1 lack quantification, scale bars.

Added quantification.

(2) Figure 2:

(a) Figure 2A, Figure 2 - Supplement 3: What are the details of the hierarchical clustering? What metric was used to decide on the number of clusters? 

We have used FANC packages to perform NBLAST clustering (Azevedo et al., 2024, Nature). We now include the full protocol in Methods.  The details are as follows:

We performed hierarchical clustering on pairwise NBLAST similarity scores computed using navis.nblast_allbyall(). The resulting similarity matrix was symmetrized by averaging it with its transpose, and converted into a distance matrix using the transformation:

distance=(1−similarity)\text{distance} = (1 - \text{similarity})distance=(1−similarity)

This ensures that a perfect NBLAST match (similarity = 1) corresponds to a distance of 0.

Clustering was performed using Ward’s linkage method (method='ward' in scipy.cluster.hierarchy.linkage), which minimizes the total within-cluster variance and is well-suited for identifying compact, morphologically coherent clusters.

We did not predefine the number of clusters. Instead, clusters were visualized using a dendrogram, where branch coloring is based on the default behavior of scipy.cluster.hierarchy.dendrogram(). By default, this function applies a visual color threshold at 70% of the maximum linkage distance to highlight groups of similar elements. In our dataset, this corresponded to a linkage distance of approximately 1–1.5, which visually separated morphologically distinct neuron types (Figures 2A and Figure 2—figure supplement 3A). This threshold was used only as a visual aid and not as a hard cutoff for quantitative grouping.

The Methods section says that the classification "included left-right comparisons". What does that mean? What are the implications of the authors only having proofread a subset of neurons in T1L (see below)? 

All adult leg motor neurons and 13A neurons (except one, 13A-ε) have neurite arbors restricted to the local, ipsilateral neuropil associated with the nearest leg.  Although 13B neurons have contralateral cell bodies, their projections are also entirely ipsilateral. The Tuthill Lab, with contributions from our group, focused proofreading efforts on the left front neuropil (T1L) in FANC. This is also where the motor neuron to muscle mapping has been most extensively done. We reconstructed/proofread the 13A and 13B neurons from the right side as well (T1R). We see similar clustering based on morphology and connectivity here as well.  

Reconstructions lack scale bars and information on orientation (also in other figures), and the figures for the 13B analysis are not consistent with the main figure (e.g., labelling of clusters in panel B along x,y axes).

Added.  

(b) Figure 2B: Since the cosine similarity matrix's values should go from -1 to 1, why was a color map used ranging from 0 to 1? 

While cosine similarity values can theoretically range from -1 to 1, in our case, all vector entries (i.e., synaptic weights) are non-negative, as they reflect the number of synapses from each 13A neuron to its downstream targets. This means all pairwise cosine similarities fall within the 0 to 1 range. 

Why are some neurons not included in this figure, like 1g, 2b, 3c-f (also in Supplement 3)?

The few 13A neurons that don’t connect to motor neurons are not shown in the figure.

(c) Figures 2C and D: the overlaid neurites are difficult to distinguish from one another. If the point here is to show that each 13A neuron class innervates specific motor neurons, then this is not the clearest way of doing that. For instance, the legend indicates that extensors are labelled in red, and that MNs with the highest number of synapses are highlighted in red - does that work? I could not figure out what was going on. On a more general point: if two cells are connected, does that not automatically mean that they should overlap in their projection patterns?

We intended these panels to illustrate that 13A neurons synapse onto overlapping regions of motor neurons, thereby creating a spatial representation of muscle targets. However, we agree that overlapping multiple neurons in a single flat projection makes the figure difficult to interpret. We have therefore removed Figures 2C and 2D.

While neurons must overlap at least somewhere if they form a synaptic connection, the amount of their neurites that overlap can vary, and more extensive overlap suggests more possible connections. Because the synapses are computationally predicted, examining the overlap helps to confirm that these predictions are consistent.

While connected neurons must overlap locally at their synaptic sites, they do not necessarily show extensive or spatially structured overlap of their projections. For example, descending neurons or 13B interneurons may form synapses onto motor neurons without exhibiting a topographically organized projection pattern. In contrast, 13A→MN connectivity is organized in a structured manner: specialist 13A neurons align with the myotopic map of MN dendrites, whereas generalist 13As project more broadly and target MN groups across multiple leg segments, reflecting premotor synergies. This spatial organization—combining both joint-specific and multi-joint representations—was a key finding we wished to highlight, and we have revised the Results text to make this clearer.

(d) Figure 2 - Figure Supplement 1: Why are these results presented in a way that goes against the morphological clustering results, but without explanation? Clusters 1-3 seem to overlap in their connectivity, and are presented in a mixed order. Why is this ignored? Are there similar data for 13B?

The morphological clusters 1–3 do exhibit overlapping connectivity, but this is consistent with both their anatomical similarity and premotor connectivity. Specifically, Cluster 1 neurons connect to SE and TrE motor neurons, Cluster 2 connects only to TrE motor neurons, and Cluster 3 targets multiple motor pools, including SE and TrE (Figure 2—Figure Supplement 1B). This overlap is also reflected in the high pairwise cosine similarity among Clusters 1–3 shown in Figure 2B. Thus, their similar connectivity profiles align with their proximity in the NBLAST dendrogram.

Regarding 13B neurons: there is no clear correlation between morphological clusters and downstream motor targets, as shown in the cosine similarity matrix (Figure 2—figure supplement 3). Moreover, even premotor 13B neurons that fall within the same morphological cluster do not connect to the same set of motor neurons (Figure 3—figure supplement 1F). For example, 13B-2a connects to LTrM and tergo-trochanteral MNs, 13B-2b connects to TiF MNs, and 13B-2g connects to Tr-F, TiE, and tergo-T MNs. Together, these results demonstrate that 13A neurons are spatially organized in a manner that correlates with their motor neuron targets, whereas 13B neurons lack such spatially structured organization, suggesting distinct principles of connectivity for these two inhibitory premotor populations.

(e) Figure 2 - Figure Supplement 2: A comparison is made here between T1R (proofread) and T1L (largely not proofread). A general point is made here that there are "similar numbers of neurons and cluster divisions". First, no quantitative comparison is provided, making it difficult to judge whether this point is accurate. Second, glancing at the connectivity diagram, I can identify a large number of discrepancies. How should we interpret those? Can T1L be proofread? If this is too much of a burden, results should be presented with that as a clear caveat.

The 13A and 13B neurons in the T1L hemisegment are fully proofread (Lesser et al, 2024, current publication); the T1R has been extensively analyzed as well.  To compare the clustering and match identities of 13A and 13B neurons on the left and the right, We mirrored the 13A neurons from the left side and used NBLAST to match them with their counterparts on the right.

While individual synaptic counts differ between sides in the FANC dataset (T1L generally showing higher counts), the number of 13A neurons, their clustering, and the overall patterns of connectivity are largely conserved between T1L and T1R.

Importantly, each 13A cluster targets the same subset of motor neurons on both sides, preserving the overall pattern of connectivity. The largest divergence is seen in cluster 9, which shows more variable connectivity.  

(f) Figure 2 - Figure Supplements 4 & 5: Why did the authors choose to present the particular cell type in Supplement 4?  Why are the cell types in Supplement 5 presented differently? Labels in Supplement 5 are illegible, but I imagine this is due to the format of the file presented to reviewers. Why are there no data for 13B?

We chose to present the particular cell type in Supplement 4 because it corresponds to cell types targeted in the genetic lines used in our behavioral experiments. The 13A neuron shown is also one of the primary neurons in this lineage. This example illustrates its broader connectivity beyond the inhibitory and motor connections emphasized in the main figures.

In Supplement 5, we initially aimed to highlight that the major downstream targets of 13A neurons are motor neurons. We have now removed this figure and instead state in the text that the major downstream targets are MNs.

We did not present 13B neurons in the same format because their major downstream targets are not motor neurons. Instead, we emphasize their role in disinhibition and their connections to 13A neurons, as shown in a specific example in Figure 3—figure supplement 2. This 13B neuron also corresponds to a cell type targeted in the genetic line used in our behavioral experiments.

(3) Figure 3:

(a) Figure 3A: the collection of diagrams is not clear. I'd suggest one diagram with all connections included repeated for each subpanel, with each subpanel highlighting relevant connections and greying out irrelevant ones to the type of connection discussed. The nomenclature should be consistent between the figure and the legend (e.g., feedforward inhibition vs direct MN inhibition in A1.

The intent of Figure 3A is to highlight individual circuit motifs by isolating them in separate panels. Including all connections in every sub panel would likely reduce clarity and make it harder to follow each motif. For completeness, we show the full set of connections together in Panel D. We updated the nomenclature as suggested. 

(b) Figure 3B: Why was the medial joint discussed in detail? Do the thicknesses of the lines represent the number of synapses? There should be a legend, in that case. Why are the green edges all the same thickness? Are they indeed all connected with a similarly low number of synapses?

We focused on the medial joint (femur-tibia joint) because it produces alternating flexion and extension of the tibia during both head sweeps and leg rubbing, which are the main grooming actions we analyzed. During head grooming, the tarsus is typically suspended in the air, so the cleaning action is primarily driven by tibial movements generated at the medial joint. 

The thickness of the edges represents the number of synapses, and we have now clarified this in the legend. The green edges represent connections from 13B neurons, which were manually added to the graph, as described in the Methods section. 13B neurons are smaller than 13A neurons and form significantly fewer total downstream synapses. For example, the 13B neuron shown in Figure 3—figure supplement 2 makes a total of 155 synapses to all downstream neurons, with only 22 synapses to its most strongly connected partner, a 13A neuron. The relatively sparse connectivity of 13B neurons is shown in thinner or uniform edge weights in this graph.

(C) Figure 3C: This is a potentially important panel, but the connections are difficult to interpret. Moreover, the text says, "This organizational motif applies to multiple joints within a leg as reciprocal connections between generalist 13A neurons suggest a role in coordinating multi-joint movements in synergy". To what extent is this a representative result? The figure also has an error in the legend (it is not labelled as 3C).

This statement is true and based on the connectivity of these neurons. We now added

“Data for 13A-MN connections shown in Figure 2—figure supplement 1 I9, I6, I7, H9, H4, and H5; 13A-13A connections shown in Figure 3—figure supplement 1C.” to the figure legend.

Thanks, we fixed the labelling error.

(d) Figure 3 - Figure Supplement 1: Panel A is very difficult to interpret. Could a hierarchical diagram be used, or some other representation that is easier to digest?

Panel A provides a consolidated view of all upstream and downstream interconnections among individual 13A and 13B neurons, allowing readers to quickly assess which neurons connect to which others without having to examine all subpanels. For a hierarchical representation, we have provided individual neuron-level diagrams in Panels C–F. 

(e) Figure 3 - Figure Supplement 2: Why was this cell type selected?

We selected this 13B because it is involved in the disinhibition of 13A neurons and is also present in the genetic line used for our behavioral experiments. 

(f) Figure 3 - Figure Supplement 3: The diagram is confusing, with text aligned randomly, and colors lacking some explanations. Legend has odd formatting.

The diagram layout and text alignment are designed to reflect the logical grouping of proprioceptors, 13A neurons, and motor neurons. To improve clarity, we have added node colors, included a written explanation for edge colors, and corrected the formatting of the figure legend.

(4) Figure 4:

(a) Figure 4A: This has no quantification, poor labelling, and odd units (centiseconds?). The colours between the left and right panels also don't align.

We have fixed these issues.

(b) Figure 4D-K: The ranges on the different axes are not the same (e.g., y axis on box plots, x axis on histograms). This obscures the fact that the differences between experimental and control, which in many cases are not big, are not consistent between the various controls. Moreover, the data that are plotted are, as far as I can tell (which is also to say: this should be explained), one value per frame. With imaging at 100Hz, this means that an enormous number of values are used in each analysis. Very small differences can therefore be significant in a statistical sense. However, how different something is between conditions is important (effect size), and this is not taken int account in this manuscript. For instance, in 4D-J, the differences in the mean seem to be minimal. Should that not be taken into consideration? A point in case is panel D in Figure 4 - Figure Supplement 1: even with near identical distributions, a statistically significant difference is detected. The same applies to Figure 4 - Figure Supplements 1-3. Also, what do the boxes and whiskers in the box plots show, exactly?

We have re-plotted all summary panels using linear mixed-effects models (LMMs) as suggested. In the updated plots, each dot represents the mean value for a single animal, and bar height represents the group mean. Whiskers indicate the 95% confidence interval around the group mean. This approach avoids inflating sample size by using per-frame values and provides a more accurate view of both variability and effect size. 

(e) Figure 4 - Figure Supplement 1: There are 6 cells labelled in the split line; only 4 are shown in A3. Is cluster 6 a convincing match between EM and MCFO?

We indeed report four neurons targeted by the split-GAL4 line in flip out clones. Generating these clones was technically challenging. In our sample (n=23), we may not have labeled all of the neurons.  Alternatively, two neurons may share very similar morphology and connectivity, making it difficult to tell them apart. We have added this clarification to the revised figure legend.

It is interesting to see data on walking in panel K, but why were these analyses not done on any of the other manipulations? What defect produced the reduction in velocity, exactly? How should this be interpreted?

Our primary focus was on grooming, but we did observe changes in walking, so we report illustrative examples. We initially included a panel showing increased walking velocity upon 13A activation, but this effect did not survive FDR correction and was removed in the revised version. We instead included data for 13A silencing which did not affect the frequency of joint movements during walking. However, spatial aspects of walking were affected: the distance between front leg tips during stance was reduced, indicating that although flies continued to walk rhythmically, the positioning of the legs was altered. This suggests that these specific 13A neurons may influence coordination and limb placement during walking without disrupting basic rhythmicity. As reviewer #2 also noted, dust may itself affect walking, so we have chosen not to further pursue this aspect in the current study.

(f) Figure 4 - Figure Supplement 2: panel A is identical to Figure 1 - Figure Supplement 1C. This figure needs particular attention, both in content and style. Why present data on silencing these neurons in C-D, but not in E-F?

We removed the panel Figure 1 - Figure Supplement 1C and kept it in Figure 4 - Figure Supplement 2 A. E-F also shows data on silencing, as C’.

(g) Figure 4 - Figure Supplement 3: In panel B, the authors should more clearly demonstrate the identity of 4b and 4a. Why present such a limited number of parameters in F and G?

The cells shown in panel B represent the best matches we could identify between the light-level expression pattern and EM reconstructions. In panels F and G, we focused on bout duration, as leg position/inter-leg distance and frequency were already presented (in Figure 4). Together, these parameters demonstrate the role of 13B neurons in coordinating leg movements. Maximum angular velocity of proximal joints was not significantly affected and is therefore not included.

(5) Figure 5:

(a) Figure 5B: Lacks a quantification of the periodic nature of the behavior, which is required to compare to experimental conditions, e.g., in panel C.

Added

(b) Figure 5C: Requires a quantification; stimulus dynamics need to be incorporated.

Added

(c) Figure 5D: More information is needed. Does "Front leg" mean "leg rub", and "Head" "head sweep"? How do the dynamics in these behaviors compare to normal grooming behavior?

Yes, head grooming is head sweeps and Front leg grooming is leg rub. Comparison added, shown in 5E-F

(d) Figure 5E: How should we interpret these plots? Do these look like normal grooming/walking?

We have now included the comparison.

(e) Figure 5F: Needs stats to compare it to 5B'.

Done

(6) Figure 6:

(a) Figure 6A: I think the circuit used for the model is lacking the claw/hook extension - 13Bs connection. Any other changes? What is the rationale?

13Bs upstream of these particular 13As do not receive significant connections from claw/hook neurons (there’s only one ~5 synapses connection from one hook extension to one 13B neurons, which we neglected for the modeling purpose). 

(b) Figure 6B and C: Needs labels, legend; where is 13B?

In the figure legend we now added: “The 13B neurons in this model do not connect to each other, receive excitatory input from the black box, and only project to the 13As (inhibitory). Their weight matrix, with only two values, is not shown.” We added the colorbar and corrected the color scheme.

(c) Figure 6D-H: plots are very difficult to interpret. Units are also missing (is "Time" correct?).

The units are indeed Time in frames (of simulation). We added this to the figure and the legend. We clarified the units of all variables in these panels. Corrected the color scheme and added their meaning to the legend text.

(d) Figure 6I: I think the authors should consider presenting this in a different format.

(e)  Figure 6 J and K (also Figure Supplement): lacks labels.

We added labels for the three joints, increased the size of fonts for clarity, and added panel titles on the top.

More specific suggestions:

(1) It would be helpful if the titles of all figures reflected the take-away message, like in Figure 2.

(2) "Their dendrites occupy a limited region of VNC, suggesting common pre-synaptic inputs" - all dendrites do, so I'd suggest rephrasing to be more precise.

(3) "We propose that the broadly projecting primary neurons are generalists, likely born earlier, while specialists are mostly later-born secondary neurons" - this needs to be explained.

We added the explanation.

We propose that the broadly projecting primary neurons are generalists, likely born earlier, while specialists are mostly later-born secondary neurons. This is consistent with the known developmental sequence of hemilineages, where early-born primary neurons typically acquire larger arbors and integrate across broader premotor and motor targets, whereas later-born secondary neurons often have more spatially restricted projections and specialized roles[18,19,81,82,85]. Our morphological clustering supports this idea: generalist 13As have extensive axonal arbors spanning multiple leg segments, whereas specialist neurons are more narrowly tuned, connecting to a few MN targets within a segment. Thus, both their morphology and connectivity patterns align with the expectation from birth-order–dependent diversification within hemilineages.

(4) "We did not find any correlation between the morphology of premotor 13B and motor connections" - this needs to be explained, as morphology constrains connectivity.

We agree that morphology often constrains connectivity. However, in contrast to 13A neurons—where morphological clusters strongly predict MN connectivity—we did not observe such a correlation for 13B neurons. As we noted in our response to comment 2d, 13B neurons can form synapses onto MNs without exhibiting extensive or spatially structured overlap of their axonal projections with MN dendrites. This suggests that 13B→MN connectivity may be governed by more local, synapse-specific rules rather than by large-scale morphological positioning, in contrast to the spatially organized premotor map we observe for 13As.

(5) "Based on their connectivity, we hypothesized that continuously activating them might reduce extension and increase flexion. Conversely, silencing them might increase extension and reduce flexion." - these clear predictions are then not directly addressed in the results that follow.

We have now expanded this section.

(6) "Thus, 13A neurons regulate both spatial and temporal aspects of leg coordination" "Together, 13A and 13B neurons contribute to both spatial and temporal coordination during grooming" - are these not intrinsically linked? This needs to be explained/justified.

The spatial (leg positioning, joint angles) and temporal (frequency, rhythm) aspects are often linked, but they can be at least partially dissociated. This has been shown in other systems: for example, Argentine ants reduce walking speed on uneven terrain primarily by decreasing stride frequency while maintaining stride length (Clifton et al., 2020), and Drosophila larvae adjust crawling speed mainly by modulating cycle period rather than the amplitude of segmental contractions (Heckscher et al., 2012). Consistent with these findings, we observe that 13A neuron manipulation in dusted flies significantly alters leg positioning without changing the frequency of walking cycles. Thus, leg positioning can be perturbed while the number of extension–flexion cycles per second remains constant, supporting the view that spatial and temporal features are at least partially dissociable.

(7) "Connectome data revealed that 13B neurons disinhibit motor pools (...) One of these 13B neurons is premotor, inhibiting both proximal and tibia extensor MN" - these are not possible at the same time.

We show that the 13B population contains neurons with distinct connectivity motifs:

some inhibit premotor 13A neurons (leading to disinhibition of motor pools), while others directly inhibit motor neurons. The split-GAL4 line we use labels three 13B neurons—two that inhibit the primary 13A neuron 13A-9d-γ (which targets proximal extensor and medial flexor MNs) and one that is premotor, directly inhibiting both proximal and tibia extensor MNs. Although these functions may appear mutually exclusive, their combined action could converge to a similar outcome: disinhibition of proximal extensor and medial flexor MNs while simultaneously inhibiting medial extensor MNs. This suggests that the labeled 13B neurons act in concert to bias the network toward a specific motor state rather than producing contradictory effects.

(8) "we often observed that one leg became locked in flexion while the other leg remained extended, (indicating contribution from additional unmapped left right coordination circuits)." - Are these results not informative? I'd suggest the authors explain the implications of this more, rather than mentioning it within brackets like this.

We agree with the reviewer that these results are highly informative. The observation that one leg can remain locked in flexion while the other stays extended suggests that additional left–right coordination circuits are engaged during grooming. This cross-talk is likely mediated by commissural interneurons downstream of inhibitory premotor neurons, which have not yet been systematically studied. Dissecting these circuits will require a dedicated project combining bilateral connectomic reconstruction, studying downstream targets of these commissural neurons, and functional interrogation, which is beyond the scope of the current study.

(9) "Indeed, we observe that optogenetic activation of specific 13A and 13B neurons triggers grooming movements. We also discover that" - this phrasing suggests that this has already been shown.external

We replaced ‘indeed’ with “Consistent with this connectivity,”

(10) "But the 13A circuitry can still produce rhythmic behavior even without those  sensory inputs (or when set to a constant value), although the legs become less coordinated." - what does this mean?

We can train (fine-tune) the model without the descending inputs from the “black box” and the behavior will still be rhythmic, meaning that our modeled 13A circuit alone can produce rhythmic behavior, i.e. the rhythm is not generated externally (by the “black box”). We added Figure 7 to the MS and re-wrote this paragraph. In the revised manuscript we now state: “But the 13A circuitry can still produce rhythmic behavior even without those excitatory inputs from the “black box” (or when set to a constant value), although the legs become less coordinated (because they are “unaware” of each other’s position at any time). Indeed, when we refine the model (with the evolutionary training) without the “black box” (using instead a constant input of 0.1) the behavior is still rhythmic although somewhat less sustained (Figure 7). This confirms that the rhythmic activity and behavior can emerge from the modeled pre-motor circuitry itself, without a rhythmic input.”

(11) "However, to explore the possibility of de novo emergent periodic behavior (without the direct periodic descending input) we instead varied the model's parameters around their empirically obtained values." - why do the authors not show how the model performs without tuning it first? What are the changes exactly that are happening as a result of the tuning? Are there specific connections that are lost? Do I interpret Figure 6B and C correctly when I think that some connections are lost (e.g., an SN-MN connection)? How does that compare to the text, which states that "their magnitudes must be at least 80% of the empirical weights"?

Without the fine-tuning we do not get any behavior (the activation levels saturate). So, we tolerate 20% divergence from the empirically established weights and we keep the signs the same. However, in the previous version we allowed the weights to decrease below 20% of the empirical weight (as long as the sign didn’t change) but not above (the signs were maintained and synapses were not added or removed). We thank the reviewer for observing this important discrepancy. In the current version we ensured that the model’s weights are bounded in both directions (the tolerance = 0.2), but we also partially relaxed the constraint on adjacency matrix re-scaling (see Methods, the “The fine-tuning of the synaptic weights” section, where we now clarify more precisely how the evolving model is fitted to the connectome constraints). We then re-ran the fine-tuning process. The Figure 6B and C is now corrected with the properly constrained model, as well as other panels in the figure.  We also applied a better color scheme (now, blue is inhibitory and red is excitatory) for Fig. 6B and C.

(12) "Interestingly, removing 13As-ii-MN connections to the three MNs (second row of the 13A → MN matrices in Figures 6B and C) does not have much effect on the leg movement (data not shown). It seems sufficient for this model to contract only one of the two antagonistic muscles per joint, while keeping the other at a steady state." - this is not clear.

We repeated this test with the newly fine-tuned model and re-wrote the result as follows:  “...when we remove just the 13A-i-MN connections (which control the flexors of the right leg) we likewise get a complete paralysis of the leg. However, removing the 13A-ii-MN (which control the extensors of the right leg) has only a modest effect on the leg movement. So, we need the 13A-i neurons to inhibit the flexors (via motor neurons), but not extensors, in order to obtain rhythmic movements.”

(13) The Discussion needs to reference the specific Results in all relevant sections.

We have revised the discussion to explicitly reference the specific results.

(14) "Flexors and extensors should alternate" - there are circumstances in which flexors and extensors should co-contract. For instance, co-contraction modulates joint stiffness for postural stability and helps generate forces required for fast movements.

Thanks for pointing this out. We added “However, flexor–extensor co-contraction can also be functionally relevant, such as for modulating joint stiffness during postural stabilization or for generating large forces required for fast movements (Zakotnik et al., 2006; Günzel et al., 2022; Ogawa and Yamawaki 2025). Some generalist 13A neurons could facilitate co-contraction across different leg segments, but none target antagonistic motor neurons controlling the same joint. Therefore, co-contraction within a single joint would require the simultaneous activation of multiple 13A neurons.”

(15) "While legs alternate between extension and flexion, they remain elevated during grooming. To maintain this posture, some MNs must be continuously activated while their antagonists are inactivated." - this is not necessarily correct. Small limbs, like those of Drosophila, can assume gravity-independent rest angles (10.1523/JNEUROSCI.5510-08.2009).

We added it to discussion

(16) The discussion "Spatial Mapping of premotor neurons in the nerve cord" seems to me to be making obvious points, and does not need to be included.

We have now revised this section to highlight the significance of 13A spatial organization, emphasizing premotor topographic mapping, multi-joint movement modules, and parallels to myotopic, proprioceptive, and vertebrate spinal maps.

(17) Key point, albeit a small one: "Normal activity of these inhibitory neurons is critical for grooming" - the use of the word critical is problematic, and perhaps typical of the tone of the manuscript. These animals still groom when many of these neurons are manipulated, so what does "critical" really mean?

In this instance, we now changed “critical” to “important”. We observed that silencing or activating a large number (>8) 13A neurons or few 13A and B neurons together completely abolishes grooming in dusted flies as flies get paralyzed or the limbs get locked in extreme poses. Therefore we think we have a justification for the statement that these neurons are critical for grooming.  These neurons may contribute to additional behaviors, and there may be partially redundant circuits that can also support grooming. We have revised the manuscript  with the intention of clarifying both what we have observed and the limits.

Author response:

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

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors endeavor to capture the dynamics of emotion-related brain networks. They employ slice-based fMRI combined with ICA on fMRI time series recorded while participants viewed a short movie clip. This approach allowed them to track the time course of four non-noise independent components at an effective 2s temporal resolution at the BOLD level. Notably, the authors report a temporal sequence from input to meaning, followed by response, and finally default mode networks, with significant overlap between stages. The use of ICA offers a data-driven method to identify large-scale networks involved in dynamic emotion processing. Overall, this paradigm and analytical strategy mark an important step forward in shifting affective neuroscience toward investigating temporal dynamics rather than relying solely on static network assessments

Strengths:

(1) One of the main advantages highlighted is the improved temporal resolution offered by slice-based fMRI. However, the manuscript does not clearly explain how this method achieves a higher effective resolution, especially since the results still show a 2s temporal resolution, comparable to conventional methods. Clarification on this point would help readers understand the true benefit of the approach.

(2) While combining ICA with task fMRI is an innovative approach to study the spatiotemporaldynamics of emotion processing, task fMRI typically relies on modeling the hemodynamic response (e.g., using FIR or IR models) to mitigate noise and collinearity across adjacent trials. The current analysis uses unmodeled BOLD time series, which might risk suffering from these issues.

(3) The study's claims about emotion dynamics are derived from fMRI data, which are inherently affected by the hemodynamic delay. This delay means that the observed time courses may differ substantially from those obtained through electrophysiology or MEG studies. A discussion on how these fMRI-derived dynamics relate to - or complement - is critical for the field to understand the emotion dynamics.

(4) Although using ICA to differentiate emotion elements is a convenient approach to tell a story, it may also be misleading. For instance, the observed delayed onset and peak latency of the 'response network' might imply that emotional responses occur much later than other stages, which contradicts many established emotion theories. Given the involvement of largescale brain regions in this network, the underlying reasons for this delay could be very complex.

Concerns and suggestions:

However, I have several concerns regarding the specific presentation of temporal dynamics in the current manuscript and offer the following suggestions.

(1) One selling point of this work regarding the advantages of testing temporal dynamics is the application of slice-based fMRI, which, in theory, should improve the temporal resolution of the fMRI time course. Improving fMRI temporal resolution is critical for a research project on this topic. The authors present a detailed schematic figure (Figure 2) to help readers understand it. However, I have difficulty understanding the benefits of this method in terms of temporal resolution.

(a) In Figure 2A, if we examine a specific voxel in slice 2, the slice acquisitions occur at 0.7s, 2.7s, and 4.7s, which implies a temporal resolution of 2s rather than 0.7s. I am unclear on how the temporal resolution could be 0.7s for this specific voxel. I would prefer that the authors clarify this point further, as it would benefit readers who are not familiar with this technology.

We very much appreciate these concerns as they highlight shortcomings in our explanation of the method. Please note that the main explanation of the method (and comparison with expected HRF and FIR based methods) is done in Janssen et al. (2018, NeuroImage; see further explanations in Janssen et al., 2020). However, to make the current paper more selfcontained, we provided further explanation of the Slice-Based method in Figure 2. With respect to the specific concern of the reviewer, in the hypothetical example used in Figure 2, the temporal resolution of the voxel on slice 2 is 0.7s because it combines the acquisitions from stimulus presentations across all trials. Specifically, given the specific study parameters as outlined in Figures 2A and B, slice 2 samples the state of the brain exactly 0s after stimulus presentation on trial 1 (red color), 0.7s after stimulus presentation on trial 3 (green color), and 1.3s after stimulus presentation on trial 2 (yellow color). Thus after combining data acquisitions across these three 3 stimuli presentations, slice 2 has sampled the state of the brain at timepoints that are multiples of 0.7s starting from stimulus onset. This is why we say that the theoretical maximum temporal resolution is equal to the TR divided by the number of slices (in the example 2/3 = 0.7s, in the actual experiment 3/39 = 0.08s). In the current study we used temporal binning across timepoints to reduce the temporal resolution (to 2 seconds) and improve the tSNR.

We have updated the legend of Figure 3 to more clearly explain this issue.

(b) Even with the claim of an increased temporal resolution (0.7s), the actual data (Figure 3) still appears to have a 2s resolution. I wonder what specific benefit slice-based fMRI brings in terms of testing temporal dynamics, aside from correcting the temporal distortions that conventional fMRI exhibits.

This is a good point. In the current experiment, the TR was 3s, but we extracted the fMRI signal at 2s temporal resolution, which means an increment of 33%. In this study we did not directly compare the impact of different temporal resolutions on the efficacy of detection of network dynamics. Indeed, we agree with the reviewer that there remain many unanswered questions about the issue of temporal resolution of the extracted fMRI signal and the impact on the ability to detect fMRI network dynamics. We think that questions such as those posed by the reviewer should be addressed in future studies that are directly focused on this issue. We have updated our discussion section (page 21-22) to more clearly reflect this point of view.

(2) In task-fMRI, the hemodynamic response is usually estimated using a specific model (e.g., FIR, IR model; see Lindquist et al., 2009). These models are effective at reducing noise and collinearity across adjacent trials. The current method appears to be conducted on unmodeled BOLD time series.

(a) I am wondering how the authors avoid the issues that are typically addressed by these HRF modeling approaches. For example, if we examine the baseline period (say, -4 to 0s relative to stimulus onset), the activation of most networks does not remain around zero, which could be due to delayed influences from the previous trial. This suggests that the current time course may not be completely accurate.

We thank the reviewer for highlighting this issue. Let us start by reiterating what we stated above: That there are many issues related to BOLD signal extraction and fMRI network discovery in task-based fMRI that remain poorly understood and should be addressed in future work. Such work should explore, for example, the impact of using a FIR vs Slice-based method on the discovery of networks in task-fMRI. These studies should also investigate the impact of different types of baselines and baseline durations on the extraction of the BOLD signal and network discovery. For the present purposes, our goal was not to introduce a new technique of fMRI signal extraction, but to show that the slice-based technique, in combination with ICA, can be used to study the brain’s networks dynamics in an emotional task. In other words, while we clearly appreciate the reviewer’s concerns and have several other studies underway that directly address these concerns, we believe that such concerns are better addressed in independent research. See our discussion on page 21-22 that addresses this issue.

(b) A related question: if the authors take the spatial map of a certain network and apply a modeling approach to estimate a time series within that network, would the results be similar to the current ICA time series?

Interesting point. Typically in a modeling approach the expected HRF (e.g., the double gamma function) is fitted to the fMRI data. Importantly, this approach produces static maps of the fit between the expected HRF and the data. By contrast, model-free approaches such as FIR or slice-based methods extract the fMRI signal directly from the data without making apriori assumptions about the expected shape of the signal. These approaches do not produce static maps but instead are capable of extracting the whole-brain dynamics during the execution of a task (event-related dynamics). These data-driven approaches (FIR, SliceBased, etc) are therefore a necessary first step in the analyses of the dynamics of brain activity during a task. The subsequent step involves the analyses of these complex eventrelated brain dynamics. In the current paper we suggest that a straightforward way to do this is to use ICA which produces spatial maps of voxels with similar time courses, and hence, yields insights into the temporal dynamics of whole-brain fMRI networks. As we mentioned above, combining ICA with a high temporal resolution data-driven signal is new and there are many new avenues for research in this burgeoning new field.

(3) Human emotion should be inherently fast to ensure survival, as shown in many electrophysiology and MEG studies. For example, the dynamics of a fearful face can occur within 100ms in subcortical regions (Méndez-Bértolo et al., 2016), and general valence and arousal effects can occur as early as 200ms (e.g., Grootswagers et al., 2020; Bo et al., 2022). In contrast, the time-to-peak or onset timing in the BOLD time series spans a much larger time range due to the hemodynamic delay. fMRI findings indeed add spatial precision to our understanding of the temporal dynamics of emotion, but could the authors comment on how the current temporal dynamics supplement those electrophysiology studies that operate on much finer temporal scales?

We really like this point. One way that EEG and fMRI are typically discussed is that these two approaches are said to be complementary. While EEG is able to provide information on temporal dynamics, but not spatial localization of brain activity, fMRI cannot provide information on the temporal dynamics, but can provide insights into spatial localization. Our study most directly challenges the latter part of this statement. We believe that by using tasks that highlight “slow” cognition, fMRI can be used to reveal not only spatial but also temporal information of brain activity. The movie task that we used presumably relies on a kind of “slow” cognition that takes place on longer time scales (e.g., the construction of the meaning of the scene). Our results show that with such tasks, whole-brain networks with different temporal dynamics can be separated by ICA, at odds with the claim that fMRI is only good for spatial information. One avenue of future research would be to attempt such “slow” tasks directly with EEG and try to find the electrical correlates of the networks detected in the current study.

We hope to have answered the concerns of the reviewer.

(4) The response network shows activation as late as 15 to 20s, which is surprising. Could the authors discuss further why it takes so long for participants to generate an emotional response in the brain?

We thank the reviewer for this question. Our study design was such that there was an initial movie clip that lasted 12.5s, which was then followed by a two-alternative forced-choice decision task (including a button press, 2.5s), and finally followed by a 10s rest period. We extracted the fMRI signal across this entire 25s period (actually 28s because we also took into account some uncertainty in BOLD signal duration). Network discovery using ICA then showed various networks with distinct time courses (across the 25s period), including one network (IC2 response) that showed a peak around 21s (see Figure 3). Given the properties of the spatial map (eg., activity in primary motor areas, Figure 4), as well as the temporal properties of its timecourse (e.g., peak close to the response stage of the task), we interpreted this network as related to generating the manual response in the two-alternative forced-choice decision task. Further analyses showed that this aspect of the task (e.g., deciding the emotion of the character in the movie clip) was also sensitive to the emotional content of the earlier movie clip (Figure 6 and 7).

We have further clarified this aspect of our results (see pages 16-17). We thank the reviewer for pointing this out.

(5) Related to 4. In many theories, the emotion processing stages-including perception, valuation, and response-are usually considered iterative processes (e.g., Gross, 2015), especially in real-world scenarios. The advantage of the current paradigm is that it incorporates more dynamic elements of emotional stimuli and is closer to reality. Therefore, one might expect some degree of dynamic fluctuation within the tested brain networks to reflect those potential iterative processes (input, meaning, response). However, we still do not observe much brain dynamics in the data. In Figure 5, after the initial onset, most network activations remain sustained for an extended period of time. Does this suggest that emotion processing is less dynamic in the brain than we thought, or could it be related to limitations in temporal resolution? It could also be that the dynamics of each individual trial differ, and averaging them eliminates these variations. I would like to hear the authors' comments on this topic.

We thank the reviewer for this interesting question. We are assuming the reviewer is referring to Figure 3 and not Figure 5. Indeed what Figure 3 shows is the average time course of each detected network across all subjects and trial types. This figure therefore does not directly show the difference in dynamics between the different emotions. However, as we show in further analyses that examine how emotion modulates specific aspects of the fMRI signal dynamics (time to peak, peak value, duration) of different networks, there are differences in the dynamics of these networks depending on the emotion (Figure 6 and 7). Thus, our results show that different emotions evoked by movie clips differ in their dynamics. Obviously, generalizing this to say that in general, different emotions have different brain dynamics is not straightforward and would require further study (probably using other tasks, and other emotions). We have updated the discussion section as well as the caption of Figure 3 to better explain this issue (see also comments by reviewer 2).

(6) The activation of the default mode network (DMN), although relatively late, is very interesting. Generally, one would expect a deactivation of this network during ongoing external stimulation. Could this suggest that participants are mind-wandering during the later portion of the task?

Very good point. Indeed this is in line with our interpretation. The late activity of the default mode network could reflect some further processing of the previous emotional experience. More work is required to clarify this further in terms of reflective, mind-wandering or regulatory processing. We have updated our discussion section to better highlight this issue (see page 19).

We thank the reviewer for their really insightful comments and suggestions!

Reviewer #2 (Public review):

Summary:

This manuscript examined the neural correlates of the temporal-spatial dynamics of emotional processing while participants were watching short movie clips (each 12.5 s long) from the movie "Forrest Gump". Participants not only watched each film clip, but also gave emotional responses, followed by a brief resting period. Employing fMRI to track the BOLD responses during these stages of emotional processing, the authors found four large-scale brain networks (labeled as IC0,1,2,4) were differentially involved in emotional processing. Overall, this work provides valuable information on the neurodynamics of emotional processing.

Strengths:

This work employs a naturalistic movie watching paradigm to elicit emotional experiences. The authors used a slice-based fMRI method to examine the temporal dynamics of BOLD responses. Compared to previous emotional research that uses static images, this work provides some new data and insights into how the brain supports emotional processing from a temporal dynamics view.

Thank you!

Weaknesses:

Some major conclusions are unwarranted and do not have relevant evidence. For example, the authors seemed to interpret some neuroimaging results to be related to emotion regulation. However, there were no explicit instructions about emotional regulation, and there was no evidence suggesting participants regulated their emotions. How to best interpret the corresponding results thus requires caution.

We thank the reviewer for pointing this out. We have updated the limitations section of our Discussion section (page 20) to better qualify our interpretations.

Relatedly, the authors argued that "In turn, our findings underscore the utility of examining temporal metrics to capture subtle nuances of emotional processing that may remain undetectable using standard static analyses." While this sentence makes sense and is reasonable, it remains unclear how the results here support this argument. In particular, there were only three emotional categories: sad, happy, and fear. These three emotional categories are highly different from each other. Thus, how exactly the temporal metrics captured the "subtle nuances of emotional processing" shall be further elaborated.

This is an important point. We also discuss this limitation in the “limitations” section of our Discussion (page 20). We again thank the reviewer for pointing this out.

The writing also contained many claims about the study's clinical utility. However, the authors did not develop their reasoning nor elaborate on the clinical relevance. While examining emotional processing certainly could have clinical relevance, please unpack the argument and provide more information on how the results obtained here can be used in clinical settings.

We very much appreciate this comment. Note that we did not intend to motivate our study directly from a clinical perspective (because we did not test our approach on a clinical population). Instead, our point is that some researchers (e.g., Kuppens & Verduyn 2017; Waugh et al., 2015) have conceptualized emotional disorders frequently having a temporal component (e.g., dwelling abnormally long on negative thoughts) and that our technique could be used to examine if temporal dynamics of networks are affected in such disorders. However, as we pointed out, this should be verified in future work. We have updated our final paragraph (page 22) to more clearly highlight this issue. We thank the reviewer for pointing this out.

Importantly, how are the temporal dynamics of BOLD responses and subjective feelings related? The authors showed that "the time-to-peak differences in IC2 ("response") align closely with response latency results, with sad trials showing faster response latencies and earlier peak times". Does this mean that people typically experience sad feelings faster than happy or fear? Yet this is inconsistent with ideas such that fear detection is often rapid, while sadness can be more sustained. Understandably, the study uses movie clips, which can be very different from previous work, mostly using static images (e.g., a fearful or a sad face). But the authors shall explicitly discuss what these temporal dynamics mean for subjective feelings.

Excellent point! Our results indeed showed that sad trials had faster reaction times compared to happy and fearful trials, and that this result was reflected in the extracted time-to-peak measures of the fMRI data (see Figure 8D). To us, this primarily demonstrates that, as shown in other studies (e.g., Menon et al., 1997), that gross differences detected in behavioral measures can be directly recovered from temporal measures in fMRI data, which is not trivial. However, we do not think we are allowed to make interpretations of the sort suggested by the reviewer (and to be clear: we do not make such interpretations in the paper). Specifically, the faster reaction times on sad trials likely reflect some audio/visual aspect of the movie clips that result in faster reaction times instead of a generalized temporal difference in the subjective experience of sad vs happy/fearful emotions. Presumably the speed with which emotional stimuli influence the brain depends on the context. Perhaps future studies that examine emotional responses while controlling for the audio/visual experience could shed further light on this issue. We have updated the discussion section to address the reviewer’s concern.

We thank the reviewer for the interesting points which have certainly improved our manuscript!

Reviewer #1 (Recommendations for the authors):

Minor:

(1) Please add the unit to the y-axis in Figure 7, if applicable.

Done. We have added units.

(2) Adding a note in the legend of Figure 3 regarding the meaning of the amplitude of the timeseries would be helpful.

Done. We have added a sentence further explaining the meaning of the timecourse fluctuations.

Related references:

(1) Lindquist, M. A., Loh, J. M., Atlas, L. Y., & Wager, T. D. (2009). Modeling the hemodynamic response function in fMRI: efficiency, bias, and mis-modeling. Neuroimage, 45(1), S187-S198.

(2) Méndez-Bértolo, C., Moratti, S., Toledano, R., Lopez-Sosa, F., Martínez-Alvarez, R., Mah, Y. H., ... & Strange, B. A. (2016). A fast pathway for fear in human amygdala. Nature neuroscience, 19(8), 1041-1049.

(3) Bo, K., Cui, L., Yin, S., Hu, Z., Hong, X., Kim, S., ... & Ding, M. (2022). Decoding the temporal dynamics of affective scene processing. NeuroImage, 261, 119532.

(4) Grootswagers, T., Kennedy, B. L., Most, S. B., & Carlson, T. A. (2020). Neural signatures of dynamic emotion constructs in the human brain. Neuropsychologia, 145, 106535.

(5) Gross, J. J. (2015). The extended process model of emotion regulation: Elaborations, applications, and future directions. Psychological inquiry, 26(1), 130-137.

Author response:

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

Reviewer #1 (Public review): 

“Ejdrup, Gether, and colleagues present a sophisticated simulation of dopamine (DA) dynamics based on a substantial volume of striatum with many DA release sites. The key observation is that a reduced DA uptake rate in the ventral striatum (VS) compared to the dorsal striatum (DS) can produce an appreciable "tonic" level of DA in VS and not DS. In both areas they find that a large proportion of D2 receptors are occupied at "baseline"; this proportion increases with simulated DA cell phasic bursts but has little sensitivity to simulated DA cell pauses. They also examine, in a separate model, the effects of clustering dopamine transporters (DAT) into nanoclusters and say this may be a way of regulating tonic DA levels in VS. I found this work of interest and I think it will be useful to the community. At the same time, there are a number of weaknesses that should be addressed, and the authors need to more carefully explain how their conclusions are distinct from those based on prior models.

We appreciate that the reviewer finds our work interesting and useful to the community. However, we acknowledge it is important to discuss how our conclusions are different from those reached based on previous model. Already in the original version of the manuscript we discussed our findings in relation to earlier models; however, this discussion has now been expanded. In particular, we would argue that our simulations, which included updated parameters, represent more accurate portrayals of in vivo conditions as it is now specifically stated in lines 466-487. Compared to previous models our data highlight the critical importance of different DAT expression across striatal subregions as a key determinant of differential DA dynamics and differential tonic levels in DS compared to VS. We find that these conclusions are already highlighted in the Abstract and Discussion. 

(1) The conclusion that even an unrealistically long (1s) and complete pause in DA firing has little effect on DA receptor occupancy is potentially important. The ability to respond to DA pauses has been thought to be a key reason why D2 receptors (may) have high affinity. This simulation instead finds evidence that DA pauses may be useless. This result should be highlighted in the abstract and discussed more.“

This is an interesting point. We have accordingly carried out new simulations across a range of D2R affinities to assess how this will affect the finding that even a long pause in DA firing has little effect on DR2 receptor occupancy. Interestingly, the simulations demonstrate that this finding is indeed robust across an order of magnitude in affinity, although the sensitivity to a one-second pause goes up as the affinity reaches 20 nM. The data are shown in a revised Figure S1H. For description of the results, please see revised text lines 195-197. The topic is now mentioned in the abstract as well as further commented in the Discussion in lines 500-504.

“(2) The claim of "DAT nanoclustering as a way to shape tonic levels of DA" is not very well supported at present. None of the panels in Figure 4 simply show mean steady-state extracellular DA as a function of clustering. Perhaps mean DA is not the relevant measure, but then the authors need to better define what is and why. This issue may be linked to the fact that DAT clustering is modeled separately (Figure 4) to the main model of DA dynamics (Figures 1-3) which per the Methods assumes even distribution of uptake. Presumably, this is because the spatial resolution of the main model is too coarse to incorporate DAT nanoclusters, but it is still a limitation.”

We agree with the reviewer that steady-state extracellular DA as a function of DAT clustering is a useful measure. We have therefore simulated the effects of different nanoclustering scenarios on this measure. We found that the extracellular concentrations went from approximately 15 nM for unclustered DAT to more than 30 nM in the densest clustering scenario. These results are shown in revised Figure 4F and described in the revised text in lines 337-349.

Further, we fully agree that the spatial resolution of the main model is a limitation and, ideally, that the nanoclustering should be combined with the large-scale release simulations. Unfortunately, this would require many orders of magnitude more computational power than currently available.

“As it stands it is convincing (but too obvious) that DAT clustering will increase DA away from clusters, while decreasing it near clusters. I.e. clustering increases heterogeneity, but how this could be relevant to striatal function is not made clear, especially given the different spatial scales of the models.”

Thank you for raising this important point. While it is true that DAT clustering increases heterogeneity in DA distribution at the microscopic level, the diffusion rate is, in most circumstances, too fast to permit concentration differences on a spatial scale relevant for nearby receptors. Accordingly, we propose that the primary effect of DAT nanoclustering is to decrease the overall uptake capacity, which in turn increases overall extracellular DA concentrations. Thus, homogeneous changes in extracellular DA concentrations can arise from regulating heterogenous DAT distribution. An exception to this would be the circumstance where the receptor is located directly next to a dense cluster – i.e. within nanometers. In such cases, local DA availability may be more directly influenced by clustering effects. Please see revised text in lines 354-362 for discussion of this matter.  

“(3) I question how reasonable the "12/40" simulated burst firing condition is, since to my knowledge this is well outside the range of firing patterns actually observed for dopamine cells. It would be better to base key results on more realistic values (in particular, fewer action potentials than 12).”

We fully agree that this typically is outside the physiological range. The values are included in addition to more realistic values (3/10 and 6/20) to showcase what extreme situations would look like. 

“(4) There is a need to better explain why "focality" is important, and justify the measure used.”

We have expanded on the intention of this measure in the revised manuscript (please see lines 266-268).  Thank you for pointing out this lack of clarification.  

“(5) Line 191: " D1 receptors (-Rs) were assumed to have a half maximal effective concentration (EC50) of 1000 nM" The assumptions about receptor EC50s are critical to this work and need to be better justified. It would also be good to show what happens if these EC50 numbers are changed by an order of magnitude up or down.”

We agree that these assumptions are critical. Simulations on effective off-rates across a range of EC50 values has now been included in the revised version in Figure 1I and is referred to in lines 188-189.  

“(6) Line 459: "we based our receptor kinetics on newer pharmacological experiments in live cells (Agren et al., 2021) and properties of the recently developed DA receptor-based biosensors (Labouesse & Patriarchi, 2021). Indeed, these sensors are mutated receptors but only on the intracellular domains with no changes of the binding site (Labouesse & Patriarchi, 2021)" 

This argument is diminished by the observation that different sensors based on the same binding site have different affinities (e.g. in Patriarchi et al. 2018, dLight1.1 has Kd of 330nM while dlight1.3b has Kd of 1600nM).”

We sincerely thank the reviewer for highlighting this important point. We fully recognize the fundamental importance of absolute and relative DA receptor kinetics for modeling DA actions and acknowledge that differences in affinity estimates from sensor-based measurements highlight the inherent uncertainty in selecting receptor kinetics parameters. While we have based our modeling decisions on what we believe to be the most relevant available data, we acknowledge that the choice of receptor kinetics is a topic of ongoing debate. Importantly, we are making our model available to the research community, allowing others to test their own estimates of receptor kinetics and assess their impact on the model’s behavior. In the revised manuscript, we have further elaborated the rationale behind our parameter choices. Please see revised text in lines in lines 177-178 of the Results section and in lines 481-486 of the Discussion. 

“(7) Estimates of Vmax for DA uptake are entirely based on prior fast-scan voltammetry studies (Table S2). But FSCV likely produces distorted measures of uptake rate due to the kinetics of DA adsorption and release on the carbon fiber surface.”

We fully agree that this is a limitation of FSCV. However, most of the cited papers attempt to correct for this by way of fitting the output to a multi-parameter model for DA kinetics. If newer literature brings the Vmax values estimated into question, we have made the model publicly available to rerun the simulations with new parameters.

“(8) It is assumed that tortuosity is the same in DS and VS - is this a safe assumption?”

The original paper cited does not specify which region the values are measured in. However, a separate paper estimates the rat cerebellum has a comparable tortuosity index (Nicholson and Phillips, J Physiol. 1981), suggesting it may be a rather uniform value across brain regions. This is now mentioned in lines 98-99 and the reference has been included. 

“(9) More discussion is needed about how the conclusions derived from this more elaborate model of DA dynamics are the same, and different, to conclusions drawn from prior relevant models (including those cited, e.g. from Hunger et al. 2020, etc)”.

As part of our revision, we have expanded the current discussion of our finding in the context of previous models in the manuscript in lines 466-487.

Reviewer #2 (Public review): 

The work presents a model of dopamine release, diffusion, and reuptake in a small (100 micrometers^2 maximum) volume of striatum. This extends previous work by this group and others by comparing dopamine dynamics in the dorsal and ventral striatum and by using a model of immediate dopamine-receptor activation inferred from recent dopamine sensor data. From their simulations, the authors report two main conclusions. The first is that the dorsal striatum does not appear to have a sustained, relatively uniform concentration of dopamine driven by the constant 4Hz firing of dopamine neurons; rather that constant firing appears to create hotspots of dopamine. By contrast, the lower density of release sites and lower rate of reuptake in the ventral striatum creates a sustained concentration of dopamine. The second main conclusion is that D1 receptor (D1R) activation is able to track dopamine concentration changes at short delays but D2 receptor activation cannot. 

The simulations of the dorsal striatum will be of interest to dopamine aficionados as they throw some doubt on the classic model of "tonic" and "phasic" dopamine actions, further show the disconnect between dopamine neuron firing and consequent release, and thus raise issues for the reward-prediction error theory of dopamine. 

There is some careful work here checking the dependence of results on the spatial volume and its discretisation. The simulations of dopamine concentration are checked over a range of values for key parameters. The model is good, the simulations are well done, and the evidence for robust differences between dorsal and ventral striatum dopamine concentration is good. 

However, the main weakness here is that neither of the main conclusions is strongly evidenced as yet. The claim that the dorsal striatum has no "tonic" dopamine concentration is based on the single example simulation of Figure 1 not the extensive simulations over a range of parameters. Some of those later simulations seem to show that the dorsal striatum can have a "tonic" dopamine concentration, though the measurement of this is indirect. It is not clear why the reader should believe the example simulation over those in the robustness checks, for example by identifying which range of parameter values is more realistic.”

We appreciate that the reviewer finds our work interesting and carefully performed.The reviewer is correct that DA dynamics, including the presence and level of tonic DA, are parameter-dependent in both the dorsal striatum (DS) and ventral striatum (VS). Indeed, our simulations across a broad range of biological parameters were intended to help readers understand how such variation would impact the model’s outcomes, particularly since many of the parameters remain contested. Naturally, altering these parameters results in changes to the observed dynamics. However, to derive possible conclusions, we selected a subset of parameters that we believe best reflect the physiological conditions, as elaborated in the manuscript. In response to the reviewer’s comment, we have placed greater emphasis on clarifying which parameter values we believe reflect the physiological conditions the most (see lines 155-157 and 254-255). Additionally, we have underscored that the distinction between tonic and non-tonic states is not a binary outcome but a parameter-dependent continuum (lines 222-225)—one that our model now allows researchers to explore systematically.  Finally, we have highlighted how our simulations across parameter space not only capture this continuum but also identify the regimes that produce the most heterogeneous DA signaling, both within and across striatal regions (lines 266-268).  

“The claim that D1Rs can track rapid changes in dopamine is not well supported. It is based on a single simulation in Figure 1 (DS) and 2 (VS) by visual inspection of simulated dopamine concentration traces - and even then it is unclear that D1Rs actually track dynamics because they clearly do not track rapid changes in dopamine that are almost as large as those driven by bursts (cf Figure 1i).”

We would like to draw the attention to Figure 1I, where the claim that D1R track rapid changes is supported in more depth (Figure S1 in original manuscript - moved to main figure to highlight this in the revised manuscript). According to this figure, upon coordinated burst firing, the D1R occupancy rapidly increased as diffusion no longer equilibrated the extracellular concentrations on a timescale faster than the receptors – and D1R receptor occupancy closely tracked extracellular DA with a delay on the order of tens of milliseconds. Note that the brief increases in [DA] from uncoordinated stochastic release events from tonic firing in Figure 1H are too brief to drive D1 signaling, as the DA concentration diffuses into the remaining extracellular space on a timescale of 1-5 ms. This is faster than the receptors response rate and does not lead to any downstream signaling according to our simulations. This means D1 kinetics are rapid enough to track coordinated signaling on a ~50 ms timescale and slower, but not fast enough to respond to individual release events from tonic activity.

“The claim also depends on two things that are poorly explained. First, the model of binding here is missing from the text. It seems to be a simple bound-fraction model, simulating a single D1 or D2 receptor. It is unclear whether more complex models would show the same thing.”

We realize that this is not made clear in the methods and, accordingly, we have updated the method section to elaborate on how we model receptor binding. The model simulates occupied fraction of D1R and D2R in every single voxel of the simulation space. Please see lines 546-555.

“Second, crucial to the receptor model here is the inference that D1 receptor unbinding is rapid; but this inference is made based on the kinetics of dopamine sensors and is superficially explained - it is unclear why sensor kinetics should let us extrapolate to receptor kinetics, and unclear how safe is the extrapolation of the linear regression by an order of magnitude to get the D1 unbinding rate.”

We chose to use the sensors because it was possible to estimate precise affinities/off-rates from the fluorescent measurements. Although there might some variation in affinities that could be attributable to the mutations introduced in the sensors, the data clearly separated D1R and D2R with a D1R affinity of ~1000 nM and a D2R affinity of ~7 nM (Labouesse & Patriarchi, 2021) consistent with earlier predictions of receptor affinities. From our assessment of the literature, we found that this was the most reasonable way to estimate affinities and thereby off-rates. Importantly, the model has been made publicly available, so should new measurements arise, the simulations can be rerun with tweaks to the input parameters. To address the concern, we have also expanded a bit on the logic applied in the updated manuscript (please see lines 177-178).

Reviewing editor Comments : 

The paper could benefit from a critical confrontation not only with existing modeling work as mentioned by the reviewers, but also with existing empirical data on pauses, D2 MSN excitability, and plasticity/learning.”

We thank both the editor and the reviewers for their suggestions on how to improve the manuscript. We have incorporated further modelling on D1R and D2R response to pauses and bursts and expanded our discussion of the results in relation to existing evidence (please see our responses to the reviewers above and the revised text in the manuscript).

Reviewer #1 (Recommendations for the authors): 

“(1) Many figure panels are too small to read clearly - e.g. "cross-section over time" plots.”

We agree with the reviewer and have increased the size of panels in several of the figures.

(2) Supplementary Videos of the model in action might be useful (and fun to watch).”

Great idea. We have generated videos of both bursts in the 3D projections and the resulting D1R and D2R occupancy in 2D. The videos are included as supplementary material as Videos S1 and S2 and referred to in the text of the revised manuscript.

” (3) Line 305: " Further, the cusp-like behaviour of Vmax in VS was independent of both Q and R%..." 

It is not clear what the "cusp" refers to here.”

We agree this is a confusing sentence. We have rewritten and eliminated the use of the vague “cusp” terminology in the manuscript.

” (4) Line 311: "We therefore reanalysed data from our previously published comparison of fibre photometry and microdialysis and found evidence of natural variations in the release-uptake balance of the mice (Figure 5F,G)" This figure seems to be missing altogether.”

The manuscript missed “S” in the mentioned sentence to indicate a supplementary figure. We apologies for the confusion and have corrected the text.

(5) Figure 1: 

1b: need numbers on the color scale.”

We have added numbers in the updated manuscript.

”1c: adding an earlier line (e.g. 2ms) could be helpful?”

We have added a 2 ms line to aid the readers.

”1d: do the colors show DA concentration on the visible surfaces of the cube or some form of projection?”

The colors show concentrations on the surface. We have expanded the text to clarify this.

”1e: is this "cross-section" a randomly-selected line (i.e. 1D) through the cube?”

The cross-section is midway through the cube. We have clarified this in the text.

”1f: "density" misspelled.”

We thank the reviewer for the keen eye. The error has been corrected.

”1g: color bars indicating stimulation time would be improved if they showed the individual stimulation pulses instead.”

The burst is simulated as a Poisson distribution and individual pulses may therefore be misleading.

” Why does the burst simulation include all release sites in a 10x10x10µm cube? Please justify this parameter choice.

1h: "1/10" - the "10" is meaningless for a single pulse, right?”

Yes, we agree. 

”1i: is this the concentration for a single voxel? Or the average of voxels that are all 1µm from one specific release site?”

Thank you for pointing out the confusing language. The figure is for a voxel containing a release site (with a voxel size of 1 um in diameter).

The legend seems a bit different from the description in the main text ("within 1µm"). As it stands, I also can't tell whether the small DA peaks are related to that particular release site, or to others. 

We have updated the text to clear up the confusing language.

” (6) Figure 2: 

2h: I'm not sure that the "relative occupancy" normalized measure is the most helpful here.”

We believe the figure aids to illustrate the sphere of influence on receptors from a single burst is greater in VS than DS, suggesting DS can process information with tighter spatial control. Using a relative measure allows for more accessible comparison of the sphere of influence in a single figure. 

” (7) Figure 3: 

The schematics need improvement.

3a – would be more useful if it corresponded better to the actual simulation (e.g. we had a spatial scale shown). 

3d – is this really useful, given the number of molecules shown is so much lower than in the simulation? 

3h, 3j – need more explanation, e.g. axis labels. ”

The schematics are intended to quickly inform the readers what parameters are tuned in the following figures, and not to be exact representations. However, we agree Figures 3h and 3j need axis labels, and we have accordingly added these.

(8) Figure 4: 

4m, n were not clearly explained. 

We agree and have elaborated the explanation of these figures in the manuscript (lines 374-377.

” (9) From Figure S1 it appears that the definition of "DS" and "VS" used is above and below the anterior commissure, respectively. This doesn't seem reasonable - many if not most studies of "VS" have examined the nucleus accumbens core, which extends above the anterior commissure. Instead, it seems like the DAT expression difference observed is primarily a difference between accumbens Shell and the rest of the striatum, rather than DS vs VS.”

We assume that the reviewer refers to Figure S3 and not S1. First, we would like to highlight that we had mislabeled VMAT2 and DAT in Figure S3C (now corrected). Apologies for the confusion. Second, as for striatal subregions, we have intentionally not distinguished between different subregions of the ventral striatum. The majority of literature we base our parameters on do not specify between e.g., NAcC vs. NAcS or DLS vs. DMS. The four slices we examined in Figure 3A-C were not perfectly aligned in the accumbal region, and we therefore do not believe we can draw any conclusions between core and shell.

Reviewer #2 (Recommendations for the authors): 

(1) Modelling assumptions: 

The burst activity simulations seem conceptually flawed. How were release sites assigned to the 150 neurons? The burst activity simulations such as Figure 1g show a spatially localised release, but this means either (1) the release sites for one DA neuron are all locally clustered, or (2) only some release sites for each DA neuron are receiving a burst of APs, those release sites are close together, and the DA neurons' other release sites are not receiving the burst. Either way, this is not plausible.”

We apologize for the confusion; however, we disagree that the simulations seem conceptually flawed. It is important to note that the burst simulation is spatially restricted to investigate local DA dynamics and how well different parts of the striatum can gate spill-over and receptor activation. The conditions may mimic local action potentials generated by nicotinic receptor activation (see e.g. Liu et al. Science 2022 or Matityahu et al, Nature Comm 2023), We have accordingly expanded on this is the manuscript on lines 148-151.

(2) Data and its reporting: 

Comparison to May and Wightman data: if we're meant to compare DS and VS concentrations, then plot them together; what were the experimental results (just says "closely resembled the earlier findings")?”

Unfortunately, the quantitative values of the May and Wightman (1989) data are not publicly available. We are therefore limited to visual comparison and cannot replot the values.

” Figures S3b and c do not agree: Figure S3b shows DAT staining dropping considerably in VS; Fig 3c does not, and neither do the quoted statistics.”

We had accidentally mixed up the labels in Figure S3c. Thank you for spotting this. We have corrected this in the updated manuscript.

” How robust are the results of simulations of the same parameter set? Figures S3D and E imply 5 simulations per burst paradigm, but these are not described.”

The bursts are simulated with a Poisson distribution as described in Methods under Three-dimensional finite difference model. This induces a stochastic variation in the simulations that mimics the empirical observations (see Dreyer et al., J. Neurosci., 2010).

” I found it rather odd that the robustness of the receptor binding results is not checked across the changes in model parameters. This seems necessary because most of the changes, such as increasing the quantal release or the number of sites, will obviously increase dopamine concentration, but they do not necessarily meaningfully increase receptor activation because of saturation (and, in more complex receptor binding models, because of the number of available receptors).”

This is an excellent point. However, we decided not to address this in the present study as we would argue that such additional simulations are not a necessity for our main conclusions. Instead, we decided in the revised version to focus on simulations mirroring a range of different receptor affinities as described in detail above. 

” Figure 4H: how can unclustered simulations have a different concentration at the centre of a "cluster" than outside, when the uptake is homogenous? Why is clustering of DAT "efficient"? [line 359]”

This is a great observation. The drop is compared to the average of the simulation space. Despite no clusters, the uniform scenario still has a concentration gradient towards the surface of the varicosity. We have elaborated on this in the manuscript on lines 346-349.

” The Discussion conclusions about what D1Rs and D2Rs cannot track are not tested in the paper (e.g. ramps). Either test them or make clear what is speculation.”

An excellent point that some of the claims in the discussion were not fully supported. We have added a simulation with a chain of burst firings to highlight how the temporal integration differs between the two receptors and updated the wording in the discussion to exclude ramps as this was not explicitly tested. See lines 191-193 and Figure S1G.

” (3) Organisation of paper: 

Consistency of terminology. These terms seem to be used to describe the same thing, but it is unclear if they are: release sites, active terminals (Table 1), varicosity density. Likewise: release probability, release fraction.”

Thank you for pointing this out. We have revised the manuscript and cleared up terminology on release sites. However, release probability and release-capable fraction of varicosities are two separate concepts.

” The references to the supplementary figure are not in sequence, and the panels assigned to the supplemental figures seem arbitrary in what is assigned to each figure and their ordering. As Figures 1 and 2 are to be directly compared, so plot the same results in each. Figure S1F is discussed as a key result, but is in a supplemental figure. ”

Thank you for identifying this. We have updated figure references and further moved Figure S1F into the main as we agree this is a main finding.

” The paper frequently reads as a loose collection of observations of simulations. For example, why look at the competitive inhibition of DA by cocaine [Fig 3H-I]? The nanoclustering of DAT (Figure 4) seems to be partial work from a different paper - it is unclear why the Vmax results warrant that detailed treatment here, especially as no rationale is offered for why we would want Vmax to change.”

We apologize if the paper reads as a loose collection of observations of simulations. This is certainly not the case. As for the cocaine competition, we used this because this modulates the Km value for DA and because we wanted to examine how dependent the dopamine dynamics are to changing different parameters in the model (Km in this case). We noticed Vmax had a separate effect between DS and VS. Accordingly, we gave it particular focus because it is physiological parameter than be modified and, if modified, it can have potential large impact on striatal DA dynamics.  Importantly, it is well known that the DA transporter (DAT) is subject to cellular regulation of its surface expression e.g. by internalization /recycling and thereby of uptake capacity (Vmax). Furthermore, we demonstrate in the present study evidence that uptake capacity on a much faster time scale can be modulated by nanoclustering, which posits a potentially novel type of synaptic plasticity. We find this rather interesting and decided therefore to focus on this in the manuscript. 

” What are the axes in Figure 3H and Figure 3J?”

We have updated the figures to include axis. Thank you for pointing out this omission.

” Much is made of the sensitivity to Vmax in VS versus DS, but this was hard work to understand. It took me a while to work out that Figure 3K was meant to indicate the range of Vmax that would be changed in VS and DS respectively. "Cusp-like behaviour" (line 305) is unclear.”

We agree that the original language was unclear – including the terminology “cusplike behavior”. We have updated the description and cut the confusion terminology. See line 366.

” The treatment of highly relevant prior work, especially that of Hunger et al 2020 and Dreyer et al (2010, 2014), is poor, being dismissed in a single paragraph late in the Discussion rather than explicating how the current paper's results fit into the context of that work. The authors may also want to discuss the anticipation of their conclusions by Wickens and colleagues, including dopamine hotspots (https://doi.org/10.1016/j.tins.2006.12.003) and differences between DS and VS dopamine release (https://doi.org/10.1196/annals.1390.016).”

We thank the reviewer for the suggested discussion points and have included and discussed references to the work by Wickens and colleagues (see lines 407-411 and 418-420).

” (4) Methods: 

Clarify the FSCV simulations: the function I_FSCV was convolved with the simulated [DA] signal?”

Yes. We have clarified this in the method section on lines 593-594.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public Review): 

Summary:

The authors of this study sought to define a role for IgM in responses to house dust mites in the lung. 

Strengths: 

Unexpected observation about IgM biology 

Combination of experiments to elucidate function 

Weaknesses: 

Would love more connection to human disease 

We thank the reviewer for these comments. At the time of this publication, we have not made a concrete link with human disease. While there is some anecdotal evidence of diseases such as Autoimmune glomerulonephritis, Hashimoto’s thyroiditis, Bronchial polyp, SLE, Celiac disease and other diseases in people with low IgM. Allergic disorders are also common in people with IgM deficiency, other studies have reported as high as 33-47%. The mechanisms for the high incidence of allergic diseases are unclear as generally, these patients have normal IgG and IgE levels. IgM deficiency may represent a heterogeneous spectrum of genetic defects, which might explain the heterogeneous nature of disease presentations.   

Reviewer #2 (Public Review): 

Summary: 

The manuscript by Hadebe and colleagues describes a striking reduction in airway hyperresponsiveness in Igm-deficient mice in response to HDM, OVA and papain across the B6 and BALB-c backgrounds. The authors suggest that the deficit is not due to improper type 2 immune responses, nor an aberrant B cell response, despite a lack of class switching in these mice. Through RNA-Seq approaches, the authors identify few di]erences between the lungs of WT and Igm-deficient mice, but see that two genes involved in actin regulation are greatly reduced in IgM-deficient mice. The authors target these genes by CRISPR-Cas9 in in vitro assays of smooth muscle cells to show that these may regulate cell contraction. While the study is conceptually interesting, there are a number of limitations, which stop us from drawing meaningful conclusions. 

Strengths:

Fig. 1. The authors clearly show that IgMKO mice have striking reduced AHR in the HDM model, despite the presence of a good cellular B cell response. 

Weaknesses: 

Fig. 2. The authors characterize the cd4 t cell response to HDM in IGMKO mice.They have restimulated medLN cells with antiCD3 for 5 days to look for IL-4 and IL-13, and find no discernible di]erence between WT and KO mice. The absence of PBStreated WT and KO mice in this analysis means it is unclear if HDM-challenged mice are showing IL-4 or IL-13 levels above that seen at baseline in this assay. 

We thank the Reviewer for this comment. We would like to mention that a very minimal level of IL-4 and IL-13 in PBS mice was detected. We have indicated with a dotted line on the Figure 2B to show levels in unstimulated or naïve cytokines. Please see Author response image 1 below from anti-CD3 stimulated cytokine ELISA data. The levels of these cytokines are very low (not detectable) and are not changed in control WT and IgM- KO mice challenge with PBS, this is also true for PMA/ionomycin-stimulated cells

Author response image 1.

The choice of 5 days is strange, given that the response the authors want to see is in already primed cells. A 1-2 day assay would have been better. 

We agree with the reviewer that a shorter stimulation period would work. Over the years we have settled for 5-day re-stimulation for both anti-CD3 and HDM. We have tried other time points, but we consistently get better secretion of cytokines after 5 days. 

It is concerning that the authors state that HDM restimulation did not induce cytokine production from medLN cells, since countless studies have shown that restimulation of medLN would induce IL-13, IL-5 and IL-10 production from medLN. This indicates that the sensitization and challenge model used by the authors is not working as it should. 

We thank the reviewer for this observation. In our recent paper showing how antigen load a]ects B cell function, we used very low levels of HDM to sensitise and challenge mice (1 ug and 3 ug respectively). See below article, Hadebe et al., 2021 JACI. This is because Labs that have used these low HDM levels also suggested that antigen load impacts B cell function, especially in their role in germinal centres. We believe the reason we see low or undetectable levels of cytokines is because of this low antigen load sensitisation and challenge. In other manuscripts we have published or about to publish, we have shown that normal HDM sensitisation load (1 ug or 100 ug) and challenge (10 ug) do induce cytokine release upon restimulation with HDM. See the below article by Khumalo et al, 2020 JCI Insight (Figure 4A).

Sabelo Hadebe*, Jermaine Khumalo, Sandisiwe Mangali, Nontobeko Mthembu, Hlumani Ndlovu, Amkele Ngomti, Martyna Scibiorek, Frank Kirstein, Frank Brombacher*. Deletion of IL-4Ra signalling on B cells limits hyperresponsiveness depending on antigen load. doi.org/10.1016/j.jaci.2020.12.635).

Jermaine Khumalo, Frank Kirstein, Sabelo Hadebe*, Frank Brombacher*. IL-4Rα signalling in regulatory T cells is required for dampening allergic airway inflammation through inhibition of IL-33 by type 2 innate lymphoid cells. JCI Insight. 2020 Oct 15;5(20):e136206. doi: 10.1172/jci.insight.136206

The IL-13 staining shown in panel c is also not definitive. One should be able to optimize their assays to achieve a better level of staining, to my mind. 

We agree with the reviewer that much higher IL-13-producing CD4 T cells should be observed. We don’t think this is a technical glitch or non-optimal set-up as we see much higher levels of IL-13-producing CD4 T cells when using higher doses of HDM to sensitise and challenge, say between 7 -20% in WT mice (see Author response image 2 of lung stimulated with PMA/ionomycin+Monensin, please note this is for illustration purposes only and it not linked to the current manuscript, its merely to demonstrate a point from other experiments we have conducted in the lab).

Author response image 2.

In d-f, the authors perform a serum transfer, but they only do this once. The half life of IgM is quite short. The authors should perform multiple naïve serum transfers to see if this is enough to induce FULL AHR. 

We thank the reviewer for this comment. We apologise if this was not clear enough on the Figure legend and method, we did transfer serum 3x, a day before sensitisation, on the day of sensitisation and a day before the challenge to circumvent the short life of IgM. In our subsequent experiments, we have now used busulfan to deplete all bone marrow in IgM-deficient mice and replace it with WT bone marrow and this method restores AHR (Figure 3B).

This now appears in line 515 to 519 and reads

Adoptive transfer of naïve serum

Naïve wild-type mice were euthanised and blood was collected via cardiac puncture before being spun down (5500rpm, 10min, RT) to collect serum. Serum (200µL) was injected intraperitoneally into IgM-deficient mice. Serum was injected intraperitoneally at day -1, 0, and a day before the challenge with HDM (day 10).

The presence of negative values of total IgE in panel F would indicate some errors in calculation of serum IgE concentrations. 

We thank the reviewer for this observation. For better clarity, we have now indicated these values as undetected in Figure 2F, as they were below our detection limit.

Overall, it is hard to be convinced that IgM-deficiency does not lead to a reduction in Th2 inflammation, since the assays appear suboptimal. 

We disagree with the reviewer in this instance, because we have shown in 3 di]erent models and in 2 di]erent strains and 2 doses of HDM (high and low) that no matter what you do, Th2 remains intact. Our reason for choosing low dose HDM was based on our previous work and that of others, which showed that depending on antigen load, B cells can either be redundant or have functional roles. Since our interest was to tease out the role of B cells and specifically IgM, it was important that we look at a scenario where B cells are known to have a function (low antigen load). We did find similar findings at high dose of HDM load, but e]ects on AHR were not as strong, but Th2 was not changed, in fact in some instances Th2 was higher in IgM-deficient mice.

Fig. 3. Gene expression di]erences between WT and KO mice in PBS and HDM challenged settings are shown. PCA analysis does not show clear di]erences between all four groups, but genes are certainly up and downregulated, in particular when comparing PBS to HDM challenged mice. In both PBS and HDM challenged settings, three genes stand out as being upregulated in WT v KO mice. these are Baiap2l1, erdr1 and Chil1. 

Noted

Fig. 4. The authors attempt to quantify BAIAP2L1 in mouse lungs. It is di]icult to know if the antibody used really detects the correct protein. A BAIAP2L1-KO is not used as a control for staining, and I am not sure if competitive assays for BAIAP2L1 can be set up. The flow data is not convincing. The immunohistochemistry shows BAIAP2L1 (in red) in many, many cells, essentially throughout the section. There is also no discernible di]erence between WT and KO mice, which one might have expected based on the RNA-Seq data. So, from my perspective, it is hard to say if/where this protein is located, and whether there truly exists a di]erence in expression between wt and ko mice. 

We thank the reviewer for this comment. We are certain that the antibody does detect BAIAP2L1, we have used it in 3 assays, which we admit may show varying specificities since it’s a Polyclonal antibody. However, in our western blot (Figure 5A), the antibody detects a band at 56.7kDa, apart from what we think are isoforms. We agree that BAIAP2L1 is expressed by many cell types, including CD45+ cells and alpha smooth muscle negative cells and we show this in our Figure 5 – figure supplement 1A and B. Where we think there is a di]erence in expression between WT and IgM-deficient mice is in alpha-smooth muscle-positive cells. We have tested antibodies from di]erent companies (Proteintech and Abcam), and we find similar findings. We do not have access to BAIAP2L1 KO mice and to test specificity, we have also used single stain controls with or without secondary antibody and isotype control which show no binding in western blot and Immunofluorescence assays and Fluorescence minus one antibody in Flow cytometry, so that way we are convinced that the signal we are seeing is specific to BAIAP2L1.

Here we have also added additional Flow cytometry images using anti-BAIAP2L1 (clone 25692-1-AP) from Proteintech

Author response image 3.

Figure similar to Figure 5C and Figure 5 -figure supplement 1A and B.

Fig. 5 and 6. The authors use a single cell contractility assay to measure whether BAIAP2L1 and ERDR1 impact on bronchial smooth muscle cell contractility. I am not familiar with the assay, but it looks like an interesting way of analysing contractility at the single cell level.

The authors state that targeting these two genes with Cas9gRNA reduces smooth muscle cell contractility, and the data presented for contractility supports this observation. However, the e]iciency of Cas9-mediated deletion is very unclear. The authors present a PCR in supp fig 9c as evidence of gene deletion, but it is entirely unclear with what e]iciency the gene has been deleted. One should use sequencing to confirm deletion. Moreover, if the antibody was truly working, one should be able to use the antibody used in Fig 4 to detect BAIAP2L1 levels in these cells. The authors do not appear to have tried this. 

We thank the reviewer for these observations. We are in a process to optimise this using new polyclonal BAIAP2L1 antibodies from other companies, since the one we have tried doesn’t seem to work well on human cells via western blot. So hopefully in our new version, we will be able to demonstrate this by immunofluorescence or western blot.

Other impressions: 

The paper is lacking a link between the deficiency of IgM and the e]ects on smooth muscle cell contraction. 

The levels of IL-13 and TNF in lavage of WT and IGMKO mice could be analysed. 

We have measured Th2 cytokine IL-13 in BAL fluid and found no di]erences between IgM-deficient mice and WT mice challenged with HDM (Author response image 4 below). We could not detected TNF-alpha in the BAL fluid, it was below detection limit.

Figure legend. IL-13 levels are not changed in IgM-deficient mice in the lung. Bronchoalveolar lavage fluid in WT or IgM-deficient mice sensitised and challenged with HDM. TNF-a levels were below the detection limit.

Author response image 4.

Moreover, what is the impact of IgM itself on smooth muscle cells? In the Fig. 7 schematic, are the authors proposing a direct role for IgM on smooth muscle cells? Does IgM in cell culture media induce contraction of SMC? This could be tested and would be interesting, to my mind. 

We thank the Reviewer for these comments. We are still trying to test this, unfortunately, we have experienced delays in getting reagents such as human IgM to South Africa. We hope that we will be able to add this in our subsequent versions of the article. We agree it is an interesting experiment to do even if not for this manuscript but for our general understanding of this interaction at least in an in vitro system.

Reviewer #3 (Public Review): 

Summary: 

This paper by Sabelo et al. describes a new pathway by which lack of IgM in the mouse lowers bronchial hyperresponsiveness (BHR) in response to metacholine in several mouse models of allergic airway inflammation in Balb/c mice and C57/Bl6 mice. Strikingly, loss of IgM does not lead to less eosinophilic airway inflammation, Th2 cytokine production or mucus metaplasia, but to a selective loss of BHR. This occurs irrespective of the dose of allergen used. This was important to address since several prior models of HDM allergy have shown that the contribution of B cells to airway inflammation and BHR is dose dependent. 

After a description of the phenotype, the authors try to elucidate the mechanisms. There is no loss of B cells in these mice. However, there is a lack of class switching to IgE and IgG1, with a concomitant increase in IgD. Restoring immunoglobulins with transfer of naïve serum in IgM deficient mice leads to restoration of allergen-specific IgE and IgG1 responses, which is not really explained in the paper how this might work. There is also no restoration of IgM responses, and concomitantly, the phenotype of reduced BHR still holds when serum is given, leading authors to conclude that the mechanism is IgE and IgG1 independent. Wild type B cell transfer also does not restore IgM responses, due to lack of engraftment of the B cells. Next authors do whole lung RNA sequencing and pinpoint reduced BAIAP2L1 mRNA as the culprit of the phenotype of IgM-/- mice. However, this cannot be validated fully on protein levels and immunohistology since di]erences between WT and IgM KO are not statistically significant, and B cell and IgM restoration are impossible. The histology and flow cytometry seems to suggest that expression is mainly found in alpha smooth muscle positive cells, which could still be smooth muscle cells or myofibroblasts. Next therefore, the authors move to CRISPR knock down of BAIAP2L1 in a human smooth muscle cell line, and show that loss leads to less contraction of these cells in vitro in a microscopic FLECS assay, in which smooth muscle cells bind to elastomeric contractible surfaces. 

Strengths: 

(1) There is a strong reduction in BHR in IgM-deficient mice, without alterations in B cell number, disconnected from e]ects on eosinophilia or Th2 cytokine production.

(2) BAIAP2L1 has never been linked to asthma in mice or humans 

Weaknesses: 

(1) While the observations of reduced BHR in IgM deficient mice are strong, there is insu]icient mechanistic underpinning on how loss of IgM could lead to reduced expression of BAIAP2L1. Since it is impossible to restore IgM levels by either serum or B cell transfer and since protein levels of BAIAP2L1 are not significantly reduced, there is a lack of a causal relationship that this is the explanation for the lack of BHR in IgMdeficient mice. The reader is unclear if there is a fundamental (maybe developmental) di]erence in non-hematopoietic cells in these IgM-deficient mice (which might have accumulated another genetic mutation over the years). In this regard, it would be important to know if littermates were newly generated, or historically bred along with the KO line. 

We thank the reviewer for asking this question and getting us to think of this in a di]erent way. This prompted us to use a di]erent method to try and restore IgM function and since our animal facility no longer allows irradiation, we opted for busulfan. We present this data as new data in Figure 3. We had to go back and breed this strain and then generated bone marrow chimeras. What we have shown now with chimeras is that if we can deplete bone marrow from IgM-deficient mice and replace it with congenic WT bone marrow when we allow these mice to rest for 2 months before challenge with HDM (Figure 3 -figure supplement 1A-C) We also show that AHR (resistance and elastance) is partially restored in this way (Figure 3A and B) as mice that receive congenic WT bone marrow after chemical irradiation can mount AHR and those that receive IgM-deficient bone marrow, can’t mount AHR upon challenge with HDM. If the mice had accumulated an unknown genetic mutation in non-hematopoietic cells, the transfer of WT bone marrow would not make a di]erence. So, we don’t believe the colony could have gained a mutation that we are unaware of. We have also shipped these mice to other groups and in their hands, this strains still only behaves as an IgM only knockout mice. See their publication below.

Mark Noviski, James L Mueller, Anne Satterthwaite, Lee Ann Garrett-Sinha, Frank Brombacher, Julie Zikherman 2018. IgM and IgD B cell receptors di]erentially respond to endogenous antigens and control B cell fate. eLife 2018;7:e35074. DOI: https://doi.org/10.7554/eLife.35074

we have also added methods for bone marrow chimaeras and added results sections and new Figures related to these methods.

Methods appear in line 521-532 of the untracked version of the article.

Busulfan Bone marrow chimeras

WT (CD45.2) and IgM^-/- (CD45.2) congenic mice were treated with 25 mg/kg busulfan (Sigma-Aldrich, Aston Manor, South Africa) per day for 3 consecutive days (75 mg/kg in total) dissolved in 10% DMSO and Phosphate bu]ered saline (0.2mL, intraperitoneally) to ablate bone marrow cells. Twenty-four hours after last administration of busulfan, mice were injected intravenously with fresh bone marrow (10x10⁶ cells, 100µL) isolated from hind leg femurs of either WT (CD45.1) or IgM^-/- mice [33]. Animals were then allowed to complement their haematopoietic cells for 8 weeks. In some experiments the level of bone marrow ablation was assessed 4 days post-busulfan treatment in mice that did not receive donor cells. At the end of experiment level of complemented cells were also assessed in WT and IgM^-/- mice that received WT (CD45.1) bone marrow. 

Results appear in line 198-228 of the untracked version of the article

Replacement of IgM-deficient mice with functional hematopoietic cells in busulfan mice chimeric mice restores airway hyperresponsiveness.

We then generated bone marrow chimeras by chemical radiation using busulfan (Montecino-Rodriguez and Dorshkind, 2020). We treated mice three times with busulfan for 3 consecutive days and after 24 hrs transferred naïve bone marrow from congenic CD45.1 WT mice or CD45.2 IgM KO mice (Figure 3A and Figure 3 -figure supplement 1A). We showed that recipient mice that did not receive donor bone marrow after 4 days post-treatment had significantly reduced lineage markers (CD45⁺Sca-1⁺) or lineage negative (Lin^-) cells in the bone marrow when compared to untreated or vehicle (10% DMSO) treated mice (Figure 3 -figure supplements 1B-C). We allowed mice to reconstitute bone marrow for 8 weeks before sensitisation and challenge with low dose HDM (Figure 3A). We showed that WT (CD45.2) recipient mice that received WT (CD45.1) donor bone marrow had higher airway resistance and elastance and this was comparable to IgM KO (CD45.2) recipient mice that received donor WT (CD45.1) bone marrow (Figure 3B). As expected, IgM KO (CD45.2) recipient mice that received donor IgM KO (CD45.2) bone marrow had significantly lower AHR compared to WT (CD45.2) or IgM KO (CD45.2) recipient mice that received WT (CD45.1) bone marrow (Figure 3B). We confirmed that the di]erences observed were not due to di]erences in bone marrow reconstitution as we saw similar frequencies of CD45.1 cells within the lymphocyte populations in the lungs and other tissues (Figure 3 -figure supplement 1D). We observed no significant changes in the lung neutrophils, eosinophils, inflammatory macrophages, CD4 T cells or B cells in WT or IgM KO (CD45.2) recipient mice that received donor WT (CD45.1/CD45.2) or IgM KO (CD45.2) bone marrow when sensitised and challenged with low dose HDM (Figure 3C).

Restoring IgM function through adoptive reconstitution with congenic CD45.1 bone marrow in non-chemically irradiated recipient mice or sorted B cells into IgM KO mice (Figure 2 -figure supplement 1A) did not replenish IgM B cells to levels observed in WT mice and as a result did not restore AHR, total IgE and IgM in these mice (Figure 2 -figure supplements 1B-C). 

The 2 new figures are Figure 3 which moved the rest of the Figures down and Figure 3- figure supplement 1AD), which also moved the rest of the supplementary figures down.

Discussion appears in line 410-419 of the untracked version of the article.To resolve other endogenous factors that could have potentially influenced reduced AHR in IgM-deficient mice, we resorted to busulfan chemical irradiation to deplete bone marrow cells in IgM-deficient mice and replace bone marrow with WT bone marrow. While it is well accepted that busulfan chemical irradiation partially depletes bone marrow cells, in our case it was not possible to pursue other irradiation methods due to changes in ethical regulations and that fact that mice are slow to recover after gamma rays irradiation. Busulfan chemical irradiation allowed us to show that we could mostly restore AHR in IgM-deficient recipient mice that received donor WT bone marrow when challenged with low dose HDM.

(2) There is no mention of the potential role of complement in activation of AHR, which might be altered in IgM-deficient mice   

We thank the reviewer for this comment. We have not directly looked at complement in this instance, however, from our previous work on C3 knockout mice, there have been comparable AHR to WT mice under the HDM challenge.

(3) What is the contribution of elevated IgD in the phenotype of the IgM-deficient mice. It has been described by this group that IgD levels are clearly elevated 

We thank the reviewer for this question. We believe that IgD is essentially what drives partial class switching to IgG, we certainly have shown that in the case of VSV virus and Trypanosoma congolense and Trypanosoma brucei brucei that elevated IgD drive delayed but e]ective IgG in the absence of IgM (Lutz et al, 2001, Nature). This is also confirmed by Noviski et al., 2018 eLife study where they show that both IgM and IgD do share some endogenous antigens, so its likely that external antigens can activate IgD in a similar manner to prompt class switching.

(4) How can transfer of naïve serum in class switching deficient IgM KO mice lead to restoration of allergen specific IgE and IgG1? 

We thank the Reviewer for these comments, we believe that naïve sera transferred to IgM deficient mice is able to bind to the surface of B cells via IgM receptors (FcμR / Fcα/μR), which are still present on B cells and this is su]icient to facilitate class switching. Our IgM KO mouse lacks both membrane-bound and secreted IgM, and transferred serum contains at least secreted IgM which can bind to surfaces via its Fc portion. We measured HDM-specific IgE and we found very low levels, but these were not di]erent between WT and IgM KO adoptively transferred with WT serum. We also detected HDM-specific IgG1 in IgM KO transferred with WT sera to the same level as WT, confirming a possible class switching, of course, we can’t rule out that transferred sera also contains some IgG1. We also can’t rule out that elevated IgD levels can partially be responsible for class switched IgG1 as discussed above.

In the discussion line 463-464, we also added the following

“We speculate that IgM can directly activate smooth muscle cells by binding a number of its surface receptors including FcμR, Fcα/μR and pIgR (Liu et al., 2019; Nguyen et al., 2017b; Shibuya et al., 2000). IgM binds to FcμR strictly, but shares Fcα/μR and pIgR with IgA (Liu et al., 2019; Michaud et al., 2020; Nguyen et al., 2017b). Both Fcα/μR and pIgR can be expressed by non-structural cells at mucosal sites (Kim et al., 2014; Liu et al., 2019). We would not rule out that the mechanisms of muscle contraction might be through one of these IgM receptors, especially the ones expressed on smooth muscle cells(Kim et al., 2014; Liu et al., 2019). Certainly, our future studies will be directed towards characterizing the mechanism by which IgM potentially activates the smooth muscle.”

We have discussed this section under Discussion section, line 731 to 757. In addition, since we have now performed bone marrow chimaeras we have further added the following in our discussion in line 410-419.

To resolve other endogenous factors that could have potentially influenced reduced AHR in IgM-deficient mice, we resorted to busulfan chemical irradiation to deplete bone marrow cells in IgM-deficient mice and replace bone marrow with WT bone marrow. While it is well accepted that busulfan chemical irradiation partially depletes bone marrow cells, in our case it was not possible to pursue other irradiation methods due to changes in ethical regulations and that fact that mice are slow to recover after gamma rays irradiation. Busulfan chemical irradiation allowed us to show that we could mostly restore AHR in IgM-deficient recipient mice that received donor WT bone marrow when challenged with low dose HDM. 

We removed the following lines, after performing bone marrow chimaeras since this changed some aspects. 

Our efforts to adoptively transfer wild-type bone marrow or sorted B cells into IgMdeficient mice were also largely unsuccessful partly due to poor engraftment of wildtype B cells into secondary lymphoid tissues. Natural secreted IgM is mainly produced by B1 cells in the peritoneal cavity, and it is likely that any transfer of B cells via bone marrow transfer would not be su]icient to restore soluble levels of IgM^3,10.

(5) lpha smooth muscle antigen is also expressed by myofibroblasts. This is insu]iciently worked out. The histology mentions "expression in cells in close contact with smooth muscle". This needs more detail since it is a very vague term. Is it in smooth muscle or in myofibroblasts. 

We appreciate that alpha-smooth muscle actin-positive cells are a small fraction in the lung and even within CD45 negative cells, but their contribution to airway hyperresponsiveness is major. We also concede that by immunofluorescence BAIAP2L1 seems to be expressed by cells adjacent to alpha-smooth muscle actin (Figure 5B), however, we know that cells close to smooth muscle (such as extracellular matrix and myofibroblasts) contribute to its hypertrophy in allergic asthma.

James AL, Elliot JG, Jones RL, Carroll ML, Mauad T, Bai TR, et al. Airway Smooth Muscle Hypertrophy and Hyperplasia in Asthma. Am J Respir Crit Care Med [Internet]. 2012; 185:1058–64. Available from: https://doi.org/10.1164/rccm.201110-1849OC

(6) Have polymorphisms in BAIAP2L1 ever been linked to human asthma? 

No, we have looked in asthma GWAS studies, at least summary statistics and we have not seen any SNPs that could be associated with human asthma.

(7) IgM deficient patients are at increased risk for asthma. This paper suggests the opposite. So the translational potential is unclear 

We thank the reviewer for these comments. At the time of this publication, we have not made a concrete link with human disease. While there is some anecdotal evidence of diseases such as Autoimmune glomerulonephritis, Hashimoto’s thyroiditis, Bronchial polyp, SLE, Celiac disease and other diseases in people with low IgM. Allergic disorders are also common in people with IgM deficiency as the reviewer correctly points out, other studies have reported as high as 33-47%. The mechanisms for the high incidence of allergic diseases are unclear as generally, these patients have normal or higher IgG and IgE levels. IgM deficiency may represent a heterogeneous spectrum of genetic defects, which might explain the heterogeneous nature of disease presentations.