I like how this reading reframed design as problem-solving rather than just visuals, because I used to think design was mostly about how things look. I also agree with the idea that everyone designs in some way, even if it isn’t professional, because it makes design feel less exclusive and more like a skill anyone can grow. The discussion about power and design justice stood out to me, and it made me think more about who gets left out when only certain people make decisions for everyone else.

I've seen many instances where people on social media will ban together to harass individuals or businesses. While often it's because these people/ businesses did something to provoke it (such as go something offensive, or offend a costumer), sometimes it can also purely be because a person online posted a video, story, tweet, etc. to tell people to go harass that person, and people than ban wagon together to do so. For example, an influencer may see someone has posted something critiquing them online, and send their fans on harass that person. While usually this isn't something where one side is completely in the right, I think online harassment as a whole is morally wrong.

Author response:

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

Reviewer #1 (Public review):

Summary

This work provides important new evidence of the cognitive and neural mechanisms that give rise to feelings of shame and guilt, as well as their transformation into compensatory behavior. The authors use a well-designed interpersonal task to manipulate responsibility and harm, eliciting varying levels of shame and guilt in participants. The study combines behavioral, computational, and neuroimaging approaches to offer a comprehensive account of how these emotions are experienced and acted upon. Notably, the findings reveal distinct patterns in how harm and responsibility contribute to guilt and shame and how these factors are integrated into compensatory decision-making.

Strengths

(1) Investigating both guilt and shame in a single experimental framework allows for a direct comparison of their behavioral and neural effects while minimizing confounds.

(2) The study provides a novel contribution to the literature by exploring the neural bases underlying the conversion of shame into behavior.

(3) The task is creative and ecologically valid, simulating a realistic social situation while retaining experimental control.

(4) Computational modeling and fMRI analysis yield converging evidence for a quotient-based integration of harm and responsibility in guiding compensatory behavior.

We are grateful for your thoughtful summary of our work’s strengths and greatly appreciate these positive words.

We would like to note that, in accordance with the journal’s requirements, we have uploaded both a clean version of the revised manuscript and a version with all modifications highlighted in blue.

Weakness

(1) Post-experimental self-reports rely both on memory and on the understanding of the conceptual difference between the two emotions. Additionally, it is unclear whether the 16 scenarios were presented in random order; sequential presentation could have introduced contrast effects or demand characteristics.

Thank you for pointing out the two limitations of the experimental paradigm. We fully agree with your point. Participants recalled and reported their feelings of guilt and shame immediately after completing the task, which likely ensured reasonably accurate state reports. We acknowledge, however, that in-task assessments might provide greater precision. We opted against them to examine altruistic decision-making in a more natural context, as in-task assessments could have heightened participants’ awareness of guilt and shame and biased their altruistic decisions. Post-task assessments also reduced fMRI scanning time, minimizing discomfort from prolonged immobility and thereby preserving data quality.

In the present study, assessing guilt and shame required participants to distinguish conceptually between the two emotions. Most research with adult participants has adopted this approach, relying on direct self-reports of emotional intensity under the assumption that adults can differentiate between guilt and shame (Michl et al., 2014; Wagner et al., 2011; Zhu et al., 2019). However, we acknowledge that this approach may be less suitable for studies involving children, who may not yet have a clear understanding of the distinction between guilt and shame.

The limitations have been added into the Discussion section (Page 47): “This research has several limitations. First, post-task assessments of guilt and shame, unlike in-task assessments, rely on memory and may thus be less precise, although in-task assessments could have heightened participants’ awareness of these emotions and biased their decisions. Second, our measures of guilt and shame depend on participants’ conceptual understanding of the two emotions. While this is common practice in studies with adult participants (Michl et al., 2014; Wagner et al., 2011; Zhu et al., 2019), it may be less appropriate for research involving children.”

We apologize for the confusion. The 16 scenarios were presented in a random order. We have clarified this in the revised manuscript (Page 13): “After the interpersonal game, the outcomes of the experimental trials were re-presented in a random order.”

(2) In the neural analysis of emotion sensitivity, the authors identify brain regions correlated with responsibility-driven shame sensitivity and then use those brain regions as masks to test whether they were more involved in the responsibility-driven shame sensitivity than the other types of emotion sensitivity. I wonder if this is biasing the results. Would it be better to use a cross-validation approach? A similar issue might arise in "Activation analysis (neural basis of compensatory sensitivity)." 

Thank you for this valuable comment. We replaced the original analyses with a leave-one-subject-out (LOSO) cross-validation approach, which minimizes bias in secondary tests due to non-independence (Esterman et al., 2010). The findings were largely consistent with the original results, except that two previously significant effects became marginally significant (one effect changed from P = 0.012 to P = 0.053; the other from P = 0.044 to P = 0.062). Although we believe the new results do not alter our main conclusions, marginally significant findings should be interpreted with caution. We have noted this point in the Discussion section (Page 48): “… marginally significant results should be viewed cautiously and warrant further examination in future studies with larger sample sizes.”

In the revised manuscript, we have described the cross-validation procedure in detail and reported the corresponding results. Please see the Method section, Page 23: “The results showed that the neural responses in the temporoparietal junction/superior temporal sulcus (TPJ/STS) and precentral cortex/postcentral cortex/supplementary motor area (PRC/POC/SMA) were negatively correlated with the responsibility-driven shame sensitivity. To test whether these regions were more involved in responsibilitydriven shame sensitivity than in other types of emotion sensitivity, we implemented a leave-one-subject-out (LOSO) cross-validation procedure (e.g., Esterman et al., 2010). In each fold, clusters in the TPJ/STS and PRC/POC/SMA showing significant correlations with responsibility-driven shame sensitivity were identified at the group level based on N-1 participants. These clusters, defined as regions of interest (ROI), were then applied to the left-out participant, from whom we extracted the mean parameter estimates (i.e., neural response values). If, in a given fold, no suprathreshold cluster was detected within the TPJ/STS or PRC/POC/SMA after correction, or if the two regions merged into a single cluster that could not be separated, the corresponding value was coded as missing. Repeating this procedure across all folds yielded an independent set of ROI-based estimates for each participant. In the LOSO crossvalidation procedure, the TPJ/STS and PRC/POC/SMA merged into a single inseparable cluster in two folds, and no suprathreshold cluster was detected within the TPJ/STS in one fold. These instances were coded as missing, resulting in valid data from 39 participants for the TPJ/STS and 40 participants for the PRC/POC/SMA. We then correlated these estimates with all four types of emotion sensitivities and compared the correlation with responsibility-driven shame sensitivity against those with the other sensitivities using Z tests (Pearson and Filon's Z).” and Page 24: “To directly test whether these regions were more involved in one of the two types of compensatory sensitivity, we applied the same LOSO cross-validation procedure described above. In this procedure, no suprathreshold cluster was detected within the LPFC in one fold and within the TP in 27 folds. These cases were coded as missing, resulting in valid data from 42 participants for the bilateral IPL, 41 participants for the LPFC, and 15 participants for the TP. The limited sample size for the TP likely reflects that its effect was only marginally above the correction threshold, such that the reduced power in cross-validation often rendered it nonsignificant. Because the sample size for the TP was too small and the results may therefore be unreliable, we did not pursue further analyses for this region. The independent ROI-based estimates were then correlated with both guilt-driven and shame-driven compensatory sensitivities, and the strength of the correlations was compared using Z tests (Pearson and Filon's Z).”

Please see the Results section, Pages 34 and 35: “To assess whether these brain regions were specifically involved in responsibility-driven shame sensitivity, we compared the Pearson correlations between their activity and all types of emotion sensitivities. The results demonstrated the domain specificity of these regions, by revealing that the TPJ/STS cluster had significantly stronger negative responses to responsibility-driven shame sensitivity than to responsibility-driven guilt sensitivity (Z = 2.44, P = 0.015) and harm-driven shame sensitivity (Z = 3.38, P < 0.001), and a marginally stronger negative response to harm-driven guilt sensitivity (Z = 1.87, P = 0.062) (Figure 4C; Supplementary Table 14). In addition, the sensorimotor areas (i.e., precentral cortex (PRC), postcentral cortex (POC), and supplementary motor area (SMA)) exhibited the similar activation pattern as the TPJ/STS (Figure 4B and 4C; Supplementary Tables 13 and 14).” and Page 35: “The results revealed that the left LPFC was more engaged in shame-driven compensatory sensitivity (Z = 1.93, P = 0.053), as its activity showed a marginally stronger positive correlation with shamedriven sensitivity than with guilt-driven sensitivity (Figure 5C). No significant difference was found in the Pearson correlations between the activity of the bilateral IPL and the two types of sensitivities (Supplementary Table 16). For the TP, the effective sample size was too small to yield reliable results (see Methods).”

(1) Regarding the traits of guilt and shame, I appreciate using the scores from the subscales (evaluations and action tendencies) separately for the analyses (instead of a composite score). An issue with using the actions subscales when measuring guilt and shame proneness is that the behavioral tendencies for each emotion get conflated with their definitions, risking circularity. It is reassuring that the behavior evaluation subscale was significantly correlated with compensatory behavior (not only the action tendencies subscale). However, the absence of significant neural correlates for the behavior evaluation subscale raises questions: Do the authors have thoughts on why this might be the case, and any implications?

We are grateful for this important comment. According to the Guilt and Shame Proneness Scale, trait guilt comprises two dimensions: negative behavior evaluations and repair action tendencies (Cohen et al., 2011). Behaviorally, both dimensions were significantly correlated with participants’ compensatory behavior (negative behavior evaluations: R = 0.39, P = 0.010; repair action tendencies: R = 0.33, P = 0.030). Neurally, while repair action tendencies were significantly associated with activity in the aMCC and other brain areas, negative behavior evaluations showed no significant neural correlates. The absence of significant neural correlates for negative behavior evaluations may be due to several factors. In addition to common explanations (e.g., limited sample size reducing the power to detect weak neural correlates or subtle effects obscured by fMRI noise), another possibility is that this dimension influences neural responses indirectly through intermediate processes not captured in our study (e.g., specific motivational states). We have added a discussion of the non-significant result to the revised manuscript (Page 47): “However, the neural correlates of negative behavior evaluations (another dimension of trait guilt) were absent. The reasons underlying the non-significant neural finding may be multifaceted. One possibility is that negative behavior evaluations influence neural responses indirectly through intermediate processes not captured in our study (e.g., specific motivational states).”

In addition, to avoid misunderstanding, the revised manuscript specifies at the appropriate places that the neural findings pertain to repair action tendencies rather than to trait guilt in general. For instance, see Pages 46 and 47: “Furthermore, we found neural responses in the aMCC mediated the relationship between repair action tendencies (one dimension of trait guilt) and compensation… Accordingly, our fMRI findings suggest that individuals with stronger tendency to engage in compensation across various moral violation scenarios (indicated by their repair action tendencies) are more sensitive to the severity of the violation and therefore engage in greater compensatory behavior.”

(2) Regarding the computational model finding that participants seem to disregard selfinterest, do the authors believe it may reflect the relatively small endowment at stake? Do the authors believe this behavior would persist if the stakes were higher?

Additionally, might the type of harm inflicted (e.g., electric shock vs. less stigmatized/less ethically charged harm like placing a hand in ice-cold water) influence the weight of self-interest in decision-making?

Taken together, the conclusions of the paper are well supported by the data. It would be valuable for future studies to validate these findings using alternative tasks or paradigms to ensure the robustness and generalizability of the observed behavioral and neural mechanisms.

Thank you for these important questions. As you suggested, we believe that the relatively small personal stakes in our task (a maximum loss of 5 Chinese yuan) likely explain why the computational model indicated that participants disregarded selfinterest. We also agree that when the harm to others is less morally charged, people may be more inclined to consider self-interest in compensatory decision-making. Overall, the more stigmatized the harm and the smaller the personal stakes, the more likely individuals are to disregard self-interest and focus solely on making appropriate compensation.

We have added the following passage to the Discussion section (Page 42): “Notably, in many computational models of social decision-making, self-interest plays a crucial role (e.g., Wu et al., 2024). However, our computational findings suggest that participants disregarded self-interest during compensatory decision-making. A possible explanation is that the personal stakes in our task were relatively small (a maximum loss of 5 Chinese yuan), whereas the harm inflicted on the receiver was highly stigmatized (i.e., an electric shock). Under conditions where the harm is highly salient and the cost of compensation is low, participants may be inclined to disregard selfinterest and focus solely on making appropriate compensation.”

Reviewer #2 (Public review):

Summary

The authors combined behavioral experiments, computational modeling, and functional magnetic resonance imaging (fMRI) to investigate the psychological and neural mechanisms underlying guilt, shame, and the altruistic behaviors driven by these emotions. The results revealed that guilt is more strongly associated with harm, whereas shame is more closely linked to responsibility. Compared to shame, guilt elicited a higher level of altruistic behavior. Computational modeling demonstrated how individuals integrate information about harm and responsibility. The fMRI findings identified a set of brain regions involved in representing harm and responsibility, transforming responsibility into feelings of shame, converting guilt and shame into altruistic actions, and mediating the effect of trait guilt on compensatory behavior.

Strengths

This study offers a significant contribution to the literature on social emotions by moving beyond prior research that typically focused on isolated aspects of guilt and shame. The study presents a comprehensive examination of these emotions, encompassing their cognitive antecedents, affective experiences, behavioral consequences, trait-level characteristics, and neural correlates. The authors have introduced a novel experimental task that enables such a systematic investigation and holds strong potential for future research applications. The computational modeling procedures were implemented in accordance with current field standards. The findings are rich and offer meaningful theoretical insights. The manuscript is well written, and the results are clearly and logically presented.

We are thankful for your considerate acknowledgment of our work’s strengths and truly value your positive comments.

We would like to note that, in accordance with the journal’s requirements, we have uploaded both a clean version of the revised manuscript and a version with all modifications highlighted in blue.

Weakness

In this study, participants' feelings of guilt and shame were assessed retrospectively, after they had completed all altruistic decision-making tasks. This reliance on memorybased self-reports may introduce recall bias, potentially compromising the accuracy of the emotion measurements.

Thank you for this crucial comment. We fully agree that measuring guilt and shame after the task may affect accuracy to some extent. However, because participants reported their emotions immediately after completing the task, we believe their recollections were reasonably accurate. In designing the experiment, we considered intask assessments, but this approach risked heightening participants’ awareness of guilt and shame and thereby interfering with compensatory decisions. After careful consideration, we ultimately chose post-task assessments of these emotions. A similar approach has been adopted in prior research on gratitude, where post-task assessments were also used (Yu et al., 2018).

In the revised manuscript, we have specified the limitations of both post-task and intask assessments of guilt and shame (Page 47): “… post-task assessments of guilt and shame, unlike in-task assessments, rely on memory and may thus be less precise, although in-task assessments could have heightened participants’ awareness of these emotions and biased their decisions.”.

In many behavioral economic models, self-interest plays a central role in shaping individual decision-making, including moral decisions. However, the model comparison results in this study suggest that models without a self-interest component (such as Model 1.3) outperform those that incorporate it (such as Model 1.1 and Model 1.2). The authors have not provided a satisfactory explanation for this counterintuitive finding. 

Thank you for this important comment. In the revised manuscript, we have provided a possible explanation (Page 42): “Notably, in many computational models of social decision-making, self-interest plays a crucial role (e.g., Wu et al., 2024). However, our computational findings suggest that participants disregarded self-interest during compensatory decision-making. A possible explanation is that the personal stakes in our task were relatively small (a maximum loss of 5 Chinese yuan), whereas the harm inflicted on the receiver was highly stigmatized (i.e., an electric shock). Under conditions where the harm is highly salient and the cost of compensation is low, participants may be inclined to disregard self-interest and focus solely on making appropriate compensation.”

The phrases "individuals integrate harm and responsibility in the form of a quotient" and "harm and responsibility are integrated in the form of a quotient" appear in the Abstract and Discussion sections. However, based on the results of the computational modeling, it is more accurate to state that "harm and the number of wrongdoers are integrated in the form of a quotient." The current phrasing misleadingly suggests that participants represent information as harm divided by responsibility, which does not align with the modeling results. This potentially confusing expression should be revised for clarity and accuracy.

We sincerely thank you for this helpful suggestion and apologize for the confusion caused. We have removed expressions such as “harm and responsibility are integrated in the form of a quotient” from the manuscript. Instead, we now state more precisely that “harm and the number of wrongdoers are integrated in the form of a quotient.”

However, in certain contexts we continue to discuss harm and responsibility. Introducing “the number of wrongdoers” in these places would appear abrupt, so we have opted for alternative phrasing. For example, on Page 3, we now write:

“Computational modeling results indicated that the integration of harm and responsibility by individuals is consistent with the phenomenon of responsibility diffusion.” Similarly, on Page 49, we state: “Notably, harm and responsibility are integrated in a manner consistent with responsibility diffusion prior to influencing guilt-driven and shame-driven compensation.”

In the Discussion, the authors state: "Since no brain region associated with social cognition showed significant responses to harm or responsibility, it appears that the human brain encodes a unified measure integrating harm and responsibility (i.e., the quotient) rather than processing them as separate entities when both are relevant to subsequent emotional experience and decision-making." However, this interpretation overstates the implications of the null fMRI findings. The absence of significant activation in response to harm or responsibility does not necessarily imply that the brain does not represent these dimensions separately. Null results can arise from various factors, including limitations in the sensitivity of fMRI. It is possible that more finegrained techniques, such as intracranial electrophysiological recordings, could reveal distinct neural representations of harm and responsibility. The interpretation of these null findings should be made with greater caution.

Thank you for this reminder. In the revised manuscript, we have provided a more cautious interpretation of the results (Page 43): “Although the fMRI findings revealed that no brain region associated with social cognition showed significant responses to harm or responsibility, this does not suggest that the human brain encodes only a unified measure integrating harm and responsibility and does not process them as separate entities. Using more fine-grained techniques, such as intracranial electrophysiological recordings, it may still be possible to observe independent neural representations of harm and responsibility.”

Reviewer #3 (Public review):

Summary

Zhu et al. set out to elucidate how the moral emotions of guilt and shame emerge from specific cognitive antecedents - harm and responsibility - and how these emotions subsequently drive compensatory behavior. Consistent with their prediction derived from functionalist theories of emotion, their behavioral findings indicate that guilt is more influenced by harm, whereas shame is more influenced by responsibility. In line with previous research, their results also demonstrate that guilt has a stronger facilitating effect on compensatory behavior than shame. Furthermore, computational modeling and neuroimaging results suggest that individuals integrate harm and responsibility information into a composite representation of the individual's share of the harm caused. Brain areas such as the striatum, insula, temporoparietal junction, lateral prefrontal cortex, and cingulate cortex were implicated in distinct stages of the processing of guilt and/or shame. In general, this work makes an important contribution to the field of moral emotions. Its impact could be further enhanced by clarifying methodological details, offering a more nuanced interpretation of the findings, and discussing their potential practical implications in greater depth.

Strengths

First, this work conceptualizes guilt and shame as processes unfolding across distinct stages (cognitive appraisal, emotional experience, and behavioral response) and investigates the psychological and neural characteristics associated with their transitions from one stage to the next.

Second, the well-designed experiment effectively manipulates harm and responsibility - two critical antecedents of guilt and shame.

Third, the findings deepen our understanding of the mechanisms underlying guilt and shame beyond what has been established in previous research.

We truly appreciate your acknowledgment of our work’s strengths and your encouraging feedback.

We would like to note that, in accordance with the journal’s requirements, we have uploaded both a clean version of the revised manuscript and a version with all modifications highlighted in blue.

Weakness

Over the course of the task, participants may gradually become aware of their high error rate in the dot estimation task. This could lead them to discount their own judgments and become inclined to rely on the choices of other deciders. It is unclear whether participants in the experiment had the opportunity to observe or inquire about others' choices. This point is important, as the compensatory decision-making process may differ depending on whether choices are made independently or influenced by external input.

Thank you for pointing this out. We apologize for not making the experimental procedure sufficiently clear. Participants (as deciders) were informed that each decider performed the dot estimation independently and was unaware of the estimations made by the other deciders. We now have clarified this point in the revised manuscript (Pages 10 and 11): “Each decider indicated whether the number of dots was more than or less than 20 based on their own estimation by pressing a corresponding button (dots estimation period, < 2.5 s) and was unaware of the estimations made by other deciders”.

Given the inherent complexity of human decision-making, it is crucial to acknowledge that, although the authors compared eight candidate models, other plausible alternatives may exist. As such, caution is warranted when interpreting the computational modeling results.

Thank you for this comment. We fully agree with your opinion. Although we tried to build a conceptually comprehensive model space based on prior research and our own understanding, we did not include all plausible models, nor would it be feasible to do so. We acknowledge it as a limitation in the revised manuscript (Page 47): “... although we aimed to construct a conceptually comprehensive computational model space informed by prior research and our own understanding, it does not encompass all plausible models. Future research is encouraged to explore additional possibilities.”

I do not agree with the authors' claim that "computational modeling results indicated that individuals integrate harm and responsibility in the form of a quotient" (i.e., harm/responsibility). Rather, the findings appear to suggest that individuals may form a composite representation of the harm attributable to each individual (i.e., harm/the number of people involved). The explanation of the modeling results ought to be precise.

We appreciate your comment and apologize for the imprecise description. In the revised manuscript, we now use the expressions “… integrate harm and the number of wrongdoers in the form of a quotient.” and “… the integration of harm and responsibility by individuals is consistent with the phenomenon of responsibility diffusion.” For example, on Page 19, we state: “It assumes that individuals neglect their self-interest, have a compensatory baseline, and integrate harm and the number of wrongdoers in the form of a quotient.” On Page 3, we state: “Computational modeling results indicated that the integration of harm and responsibility by individuals is consistent with the phenomenon of responsibility diffusion.”

Many studies have reported positive associations between trait gratitude, social value orientation, and altruistic behavior. It would be helpful if the authors could provide an explanation about why this study failed to replicate these associations.

Thanks a lot for this important comment. We have now added an explanation into the revised manuscript (Page 47): “Although previous research has found that trait gratitude and SVO are significantly associated with altruistic behavior in contexts such as donation (Van Lange et al., 2007; Yost-Dubrow & Dunham, 2018) and reciprocity (Ma et al., 2017; Yost-Dubrow & Dunham, 2018), their associations with compensatory decisions in the present study were not significant. This suggests that the effects of trait gratitude and SVO on altruistic behavior are context-dependent and may not predict all forms of altruistic behavior.”

As the authors noted, guilt and shame are closely linked to various psychiatric disorders. It would be valuable to discuss whether this study has any implications for understanding or even informing the treatment of these disorders.

We are grateful for this advice. Although our study did not directly examine patients with psychological disorders, the findings offer insights into the regulation of guilt and shame. As these emotions are closely linked to various disorders, improving their regulation may help alleviate related symptoms. Accordingly, we have added a paragraph highlighting the potential clinical relevance (Pages 48 and 49): “Our study has potential practical implications. The behavioral findings may help counselors understand how cognitive interventions targeting perceptions of harm and responsibility could influence experiences of guilt and shame. The neural findings highlight specific brain regions (e.g., TPJ) as potential intervention targets for regulating these emotions. Given the close links between guilt, shame, and various psychological disorders (e.g., Kim et al., 2011; Lee et al., 2001; Schuster et al., 2021), strategies to regulate these emotions may contribute to symptom alleviation. Nevertheless, because this study was conducted with healthy adults, caution is warranted when considering applications to other populations.”

Reviewer #1 (Recommendations for the authors):

(1) Would it be interesting to explore other categories of behavior apart from compensatory behavior?

Thanks a lot for this insightful question. We focused on a classic form of altruistic behavior, compensation. Future studies are encouraged to adapt our paradigm to examine other behaviors associated with guilt and/or shame, such as donation (Xu, 2022), avoidance (Shen et al., 2023), or aggression (Velotti et al., 2014). Please see Page 48: “Future research could combine this paradigm with other cognitive neuroscience methods, such as electroencephalography (EEG) or magnetoencephalography (MEG), and adapt it to investigate additional behaviors linked to guilt and shame, including donation (Xu, 2022), avoidance (Shen et al., 2023), and aggression (Velotti et al., 2014).”

(2) Did the computational model account for the position of the block (slider) at the start of each decision-making response (when participants had to decide how to divide the endowment)? Or are anchoring effects not relevant/ not a concern?

Thank you for this interesting question. In our task, the initial position of the slider was randomized across trials, and participants were explicitly informed of this in the instructions. This design minimized stable anchoring effects across trials, as participants could not rely on a consistent starting point. Although anchoring might still have influenced individual trial responses, we believe it is unlikely that such effects systematically biased our results, since randomization would tend to cancel them out across trials. Additionally, prior research has shown that when multiple anchors are presented, anchoring effects are reduced if the anchors contradict each other (Switzer

III & Sniezek, 1991). Therefore, we did not attempt to model potential anchoring effects. Nevertheless, future research could systematically manipulate slider starting positions to directly examine possible anchoring influences. In the revised manuscript, we have added a brief clarification (Page 11): “The initial position of the block was randomized across trials, which helped minimize stable anchoring effects across trials.”

(3) Was there a real receiver who experienced the shocks and received compensation? I think it is not completely clear in the paper.

We are sorry for not making this clear enough. The receiver was fictitious and did not actually exist. We have supplemented the Methods section with the following description (Page 12): “We told the participant a cover story that the receiver was played by another college student who was not present in the laboratory at the time. … In fact, the receiver did not actually exist.”.

(4) What was the rationale behind not having participants meet the receiver?

Thank you for this question. Having participants meet the receiver (i.e., the victim), played by a confederate, might have intensified their guilt and shame and produced a ceiling effect. In addition, the current approach simplified the experimental procedure and removed the need to recruit an additional confederate. These reasons have been added to the Methods section (Page 12): “Not having participants meet the receiver helped prevent excessive guilt and shame that might produce a ceiling effect, while also eliminating the need to recruit an additional confederate.”

Minor edits:

(1) Line 49: "the cognitive assessment triggers them", I think a word is missing.

(2) Line 227: says 'Slide' instead of 'Slider'.

(3) Lines 867/868: "No brain response showed significant correlation with responsibility-driven guilt sensitivity, harm-driven shame sensitivity, or responsibilitydriven shame sensitivity." I think it should be harm-driven guilt sensitivity, responsibility-driven guilt sensitivity, and harm-driven shame sensitivity.

(4) Supplementary Information Line 12: I think there is a typo ( 'severs' instead of 'serves')

We sincerely thank you for patiently pointing out these typos. We have corrected them accordingly. 

(1) “the cognitive assessment triggers them” has been revised to “the cognitive antecedents that trigger them” (Page 2).

(2) “SVO Slide Measure” has been revised to “SVO Slider Measure” (Page 8).

(3) “No brain response showed significant correlation with responsibility-driven guilt sensitivity, harm-driven shame sensitivity, or responsibility-driven shame sensitivity." has been revised to “No brain response showed significant correlation with harm-driven guilt sensitivity, responsibility-driven guilt sensitivity, and harm-driven shame sensitivity.” (Page 35).

(4) “severs” has been revised to “serves” (see Supplementary Information). In addition, we have carefully checked the entire manuscript to correct any remaining typographical errors.

Reviewer #2 (Recommendations for the authors):

The statement that trait gratitude and SVO were measured "for exploratory purposes" would benefit from further clarification regarding the specific questions being explored.

Thank you for this valuable suggestion. In the revised manuscript, we have illustrated the exploratory purposes (Page 9): “We measured trait gratitude and SVO for exploratory purposes. Previous research has shown that both are linked to altruistic behavior, particularly in donation contexts (Van Lange et al., 2007; Yost-Dubrow & Dunham, 2018) and reciprocity contexts (Ma et al., 2017; Yost-Dubrow & Dunham, 2018). Here, we explored whether they also exert significant effects in a compensatory context.”

In the Methods section, the authors state: "To confirm the relationships between κ and guilt-driven and shame-driven compensatory sensitivities, we calculated the Pearson correlations between them." However, the Results section reports linear regression results rather than Pearson correlation coefficients, suggesting a possible inconsistency. The authors are advised to carefully check and clarify the analysis approach used.

We thank you for the careful reviewing and apologize for this mistake. We used a linear mixed-effects regression instead of Pearson correlations for the analysis. The mistake has been revised (Page 25): “To confirm the relationships between κ and guiltdriven and shame-driven compensatory sensitivities, we conducted a linear mixedeffects regression. κ was regressed onto guilt-driven and shame-driven compensatory sensitivities, with participant-specific random intercepts and random slopes for each fixed effect included as random effects.”

A more detailed discussion of how the current findings inform the regulation of guilt and shame would further strengthen the contribution of this study.

Thank you for this suggestion. We have added a paragraph discussing the implications for the regulation of guilt and shame (Pages 48 and 49): “Our study has potential practical implications. The behavioral findings may help counselors understand how cognitive interventions targeting perceptions of harm and responsibility could influence experiences of guilt and shame. The neural findings highlight specific brain regions (e.g., TPJ) as potential intervention targets for regulating these emotions. Given the close links between guilt, shame, and various psychological disorders (e.g., Kim et al., 2011; Lee et al., 2001; Schuster et al., 2021), strategies to regulate these emotions may contribute to symptom alleviation. Nevertheless, because this study was conducted with healthy adults, caution is warranted when considering applications to other populations.”

As fMRI provides only correlational evidence, establishing a causal link between neural activity and guilt- or shame-related cognition and behavior would require brain stimulation or other intervention-based methods. This may represent a promising direction for future research.

Thank you for this advice. We also agree that it is important for future research to establish the causal relationships between the observed brain activity, psychological processes, and behavior. We have added a corresponding discussion in the revised manuscript (Pages 47 and 48): “… fMRI cannot establish causality. Future studies using brain stimulation techniques (e.g., transcranial magnetic stimulation) are needed to clarify the causal role of brain regions in guilt-driven and shame-driven altruistic behavior.”

Reviewer #3 (Recommendations for the authors):

It was mentioned that emotions beyond guilt and shame, such as indebtedness, may also drive compensation. Were any additional types of emotion measured in the study?

Thank you for this question. We did not explicitly measure emotions other than guilt and shame. However, the parameter κ from our winning computational model captures the combined influence of various psychological processes on compensation, which may reflect the impact of emotions beyond guilt and shame (e.g., indebtedness). We acknowledge that measuring other emotions similar to guilt and shame may help to better understand their distinct contributions. This point has been added into the revised manuscript (Page 48): “… we did not explicitly measure emotions similar to guilt and shame (e.g., indebtedness), which would have been helpful for understanding their distinct contributions.”

The experimental task is complicated, raising the question of whether participants fully understood the instructions. For instance, one participant's compensation amount was zero. Could this reflect a misunderstanding of the task instructions?

Thanks a lot for this question. In our study, after reading the instructions, participants were required to complete a comprehension test on the experimental rules. If they made any mistakes, the experimenter provided additional explanations. Only after participants fully understood the rules and correctly answered all comprehension questions did they proceed to the main experimental task. We have clarified this procedure in the revised manuscript (Page 13): “Participants did not proceed to the interpersonal game until they had fully understood the experimental rules and passed a comprehension test.”

Making identical choices across different trials does not necessarily indicate that participants misunderstood the rules. Similar patterns, where participants made the same choices across trials, have also been observed in previous studies (Zhong et al., 2016; Zhu et al., 2021).

Reference

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Author response:

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

Public Reviews:

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.

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. However, this is also a weakness of the work. Such thorough analysis makes it very hard to read! It's a very interesting paper with some excellent and thought provoking references but it needs to be careful not to overstate the results and improve the readability so it can be disseminated widely. It should also discuss more alternative explanations for the findings and, where possible, dismiss them.

I have toned down the language including a more neutral title. To help focus on the main results, I have moved four paragraphs from the methods to the supplement. These are the sample size, the two sensitivity analyses on including co-reviewers and confounding by reviewers’ characteristics, and the analysis examining potential bias for the reviewers with no OpenAlex record.

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.

Weaknesses:

The author needs to be more clear on the fact that, in some instances, requests for selfcitations by reviewers is important and valuable.

This is a key point. I have included a new text analysis to examine this issue and have addressed this in the updated discussion.

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 concerns pertain to the interpretability of the data as presented and the overly terse writing style.

Regarding interpretability, it is often unclear what subset of the data are being used both in the prose and figures. For example, the descriptive statistics show many more Version 1 articles than Version 2+. How are the data subset among the different possible methods?

I have now included the number of articles and reviews in the legends of each plot. There are more version 1 articles because some are “approved” at this stage and hence a second version is never submitted (I’ve now specifically mentioned this in the discussion).

Likewise, the methods indicate that a matching procedure was used comparing two reviewers for the same manuscript in order to control for potential confounds. However, the number of reviews is less than double the number of Version 1 articles, making it unclear which data were used in the final analysis. The methods also state that data were stratified by version. This raises a question about which articles/reviews were included in each of the analyses. I suggest spending more space describing how the data are subset and stratified. This should include any conditional subsetting as in the analysis on the 441 reviews where the reviewer was not cited in Version 1 but requested a citation for Version 2. Each of the figures and tables, as well as statistics provided in the text should provide this information, which would make this paper much more accessible to the reader.

[Note from editor: Please see "Editorial feedback" for more on this]

The numbers are now given in every figure legend, and show the larger sample size for the first versions.

The analysis of the 441 reviews was an unplanned analysis that is separate to the planned models. The sample size is much smaller than the main models due to the multiple conditions applied to the reviewers: i) reviewed both versions, ii) not cited in first version, iii) requested a self-citation in their first review.

Finally, I would caution against imputing motivations to the reviewers, despite the important findings provided here. This is because the data as presented suggest a more nuanced interpretation is warranted. First, the author observes similar patterns of accept/reject decisions whether the suggested citation is a citation to the reviewer or not (Figs 3 and 4). Second, 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, but largely left out of the discussion. The conditional analysis on the 441 reviews mentioned above does support a more cautious version of the conclusion drawn here, especially when considered alongside the specific comments left by reviewers that were mentioned in the results and information in Table S.3. However, I recommend toning the language down to match the strength of the data.

I have used more cautious language throughout, including a new title. The new text analysis presented in the updated version also supports a more cautious approach.

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.

Barring a few issues discussed below, 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.

It is surprising that even in these investigated journals where referee names are public, there is prevalence of such citation-related behaviors.

Weaknesses:

Some overall claims are questionable:

"Reviewers who were cited were more likely to approve the article, but only after version 1" It also appears that referees who were cited were less likely to approve the article in version 1. This null or slightly negative effect undermines the broad claim of citations swaying referees. The paper highlights only the positive results while not including the absence (and even reversal) of the effect in version 1 in its narrative.

The reversed effect for version 1 is interesting, but the adjusted 99.4% confidence interval includes 1 and hence it’s hard to be confident that this is genuinely in the reverse direction. However, it is certainly far from the strongly positive association for versions 2+.

"To the best of our knowledge, this is the first analysis to use a matched design when examining reviewer citations" Does not appear to be a valid claim based on the literature reference [18]

This previous paper used a matched design but then did not used a matched analysis. Hence, I’ve changed the text in my paper to “first analysis to use a matched design and analysis”. This may seem a minor claim of novelty, but not using a matched analysis for matched data could discard much of the benefits of the matching.

It will be useful to have a control group in the analysis associated to Figure 5 where the control group comprises matched reviews that did not ask for a self citation. This will help demarcate words associated with approval under self citation (as compared to when there is no self citation). The current narrative appears to suggest an association of the use of these words with self citations but without any control.

Thanks for this useful suggestion. I have added a control group of reviewers who requested citations to articles other than their own. The words requested were very similar to the previous analysis, hence I’ve needed to reinterpret the results from the text analysis as “please” and “need” are not exclusively used by those requesting selfcitations. I also fixed a minor error in the text analysis concerning the exclusion of abstracts of shorter than 100 characters.

More discussion on the recommendations will help:

For the suggestion that "the reviewers initially see a version of the article with all references blinded and no reference list" the paper says "this involves more administrative work and demands more from peer reviewers". I am afraid this can also degrade the quality of peer review, given that the research cannot be contextualized properly by referees. Referees may not revert back to all their thoughts and evaluations when references are released afterwards.

This is an interesting point, but I don’t think it’s certain that this would happen. For example, revisiting the review may provide a fresh perspective and new ideas; this sometimes happens for me when I review the second version of an article. Ideally an experiment is needed to test this approach, as it is difficult to predict how authors and reviewers will react.

Recommendations for the Authors:

Editorial feedback:

I wonder if the article would benefit from a shorter title, such as the one suggested below. However, please feel free to not change the title if you prefer.

[i] Are peer reviewers influenced by their work being cited (or not)?

I like the slightly simpler: “Are peer reviewers influenced by their work being cited?”

[ii] To better reflect the findings in the article, please revise the abstract along the following lines:

Peer reviewers for journals sometimes write that one or more of their own articles should have been cited in the article under review. In some cases such comments are justified, but in other cases they are not. Here, using a sample of more than 37000 peer reviews for four journals that use open peer review and make all article versions available, we use a matched study design to explore this and other phenomena related to citations in the peer review process. We find that reviewers who were cited in the article under review were less likely to approve the original version of an article compared with reviewers who were not cited (odds ratio = 0.84; adjusted 99.4% CI: 0.69-1.03), but were more likely to approve a revised article in which they were cited (odds ratio = 1.61; adjusted 99.4% CI: 1.16-2.23). Moreover, for all versions of an article, reviewers who asked for their own articles to be cited were much less likely to approve the article compared with reviewers who did not do this (odds ratio = 0.15; adjusted 99.4% CI: 0.08-0.30). However, reviewers who had asked for their own articles to be cited were much more likely to approve a revised article that cited their own articles compared to a revised article that did not (odds ratio = 3.5; 95% CI: 2.0-6.1).

I have re-written the abstract along the lines suggested. I have not included the finding that cited reviewers were less likely to approve the article due to the adjusted 99.4% interval including 1.

[iii] The use of the phrase "self-citation" to describe an author citing an article by one of the reviewers is potentially confusing, and I suggest you avoid this phrase if possible.

I have removed “self-citation” everywhere and instead used “citations to their own articles”.

[iv] I think the captions for figures 2, 3 and 4 from benefit from rewording to more clearly describe what is being shown in the figure. Please consider revising the caption for figure 2 as follows, and revising the captions for figures 3 and 4 along similar lines. Please also consider replotting some of the panels so that the values on the horizontal axes of the top panel align with the values on the bottom panel.

I have aligned the odds and probability axes as suggested which better highlights the important differences. I have updated the figure captions as outlined.

Figure 2: Odds ratios and probabilities for reviewers giving a more or less favourable recommendation depending on whether they were cited in the article.

Top left: Odds ratios for reviewers giving a more favourable (Approved) or less favourable (Reservations or Not approved) recommendation depending on whether they were cited in the article. Reviewers who were cited in version 1 of the article (green) were less likely to make a favourable recommendation (odds ratio = 0.84; adjusted 99.4% CI: 0.691.03), but they were more likely to make a favourable recommendation (odds ratio = 1.61; adjusted 99.4% CI: 1.16-2.23) if they were cited in a subsequent version (blue). Top right: Same data as top left displayed in terms of probabilities. From the top, the lines show the probability of a reviewer approving: a version 1 article in which they are not cited (please give mean value and CI); a version 1 article in which they are cited (mean value and CI); a version 2 (or higher) article in which they are not cited (mean value and CI); and a version 2 (or higher) article in which they are cited (mean value and CI).

Bottom left: Same data as top left except that more favourable is now defined as Approved or Reservations, and less favourable is defined as Not approved. Again, reviewers who were cited in version 1 were less likely to make a favourable recommendation (odds ratio = 0.84; adjusted 99.4% CI: 0.57-1.23),and reviewers who were cited in subsequent versions were more likely to make a favourable recommendation (odds ratio = 1.12; adjusted 99.4% CI: 0.59-2.13).

Bottom right: Same data as bottom left displayed in terms of probabilities. From the top, the lines show the probability of a reviewer approving: a version 1 article in which they are not cited (please give mean value and CI); a version 1 article in which they are cited (mean value and CI); a version 2 (or higher) article in which they are not cited (mean value and CI); and a version 2 (or higher) article in which they are cited (mean value and CI).

This figure is based on an analysis of [Please state how many articles, reviewers, reviews etc are included in this analysis].

In all the panels a dot represents a mean, and a horizontal line represents an adjusted 99.4% confidence interval.

Reviewer #1 (Recommendations for the Authors):

A big recommendation to the author would be to consider putting a lot of the statistical analysis in an appendix and describing the methods and results in more accessible terms in the main text. This would help more readers see the baby through the bath water

I have moved four paragraphs from the methods to the supplement. These are the sample size, the two sensitivity analyses on including co-reviewers and confounding by reviewers’ characteristics, and the analysis examining potential bias for the reviewers with no OpenAlex record.

One possibility, that may have been accounted for, but it is hard to say given the density of the analysis, is the possibility that an author who follows the recommendations to cite the reviewer has also followed all the other reviewer requests. This could account for the much higher likelihood of acceptance. Conversely an author who has rejected the request to cite the reviewer may be more likely to have rejected many of the other suggestions leading to a rejection. I couldn't discern whether the analysis had accounted for this possibility. If it has it need to be said more prominently, if it hasn't this possibility at least needs to be discussed. It would be good to see other alternative explanations for the results discussed (and if possible dismissed) in the discussion section too.

This is an interesting idea. It’s also possible that authors more often accept and include any citation requests as it gives them more license to push back on other more involved changes that they would prefer not to make, e.g., running a new analysis. To examine this would require an analysis of the authors’ responses to the reviewers, and I have now added this as a limitation.

I hope this paper will have an impact on scientific publishing but I fear that it won't. This is no reflection on the paper but a more a reflection on the science publishing system.

I do not have any additional references (written by myself or others!) I would like the author to include

Thanks. I appreciate that extra thought is needed when peer reviewing papers on peer review. I do not know the reviewers’ names! I have added one additional reference suggested by the reviewers which had relevant results on previous surveys of coercive citations for the section on “Related research”.

Reviewer #2 (Recommendations for the Authors):

(1) Would it be possible for the author to control for academic discipline? Some disciplines cite at different rates and have different citation sub-cultures; for example, Wilhite and Fong (2012) show that editorial coercive citation differs among the social science and business disciplines. Is it possible that reviewers from different disciplines just take a totally different view of requesting self-citations?

Wilhite, A.W., & Fong, E.A. 2012. Coercive citation in academic publishing. Science, 335: 542-543.

This is an interesting idea, but the number of disciplines would need to be relatively broad to keep a sufficient sample size. The Catch-22 is then whether broad disciplines are different enough to show cultural differences. Overall, this is an idea for future work.

(2) I would like the author to be much more clear about their results in the discussion section. In line 214, they state that "Reviewers who requested a self-citation were much less likely to approve the article for all versions." Maybe in the discussion some language along the lines of "Although reviewers who requested self-citation were actually much less likely to approve an article, my more detailed analyses show that this was not the case when reviewers requested a self-citation without reason or with the inclusion of coercive language such as 'need' or 'please'." Again, word it as you like, but I think it should be made clear that requests for self-citation alone is not a problem. In fact, I would argue that what the author says in lines 250 to 255 in the discussion reflects that reviewers who request self-citations (maybe for good reasons) are more likely to be the real experts in the area and why those who did not request a self-cite did not notice the omission. It is my understanding that editors are trying to get warm bodies to review and thus reviewers are not all equally qualified. Could it be that requesting self-citations for a good reason is a proxy for someone who actually knows the literature better? I'm not saying this is s fact, but it is a possibility. I get this is said in the abstract, but worth fleshing out in the discussion.

I have updated the discussion after a new text analysis and have addressed this important question of whether self-citations are different from citations to other articles. The idea that some self-citers are more aware of the relevant literature is interesting, although this is very hard to test because they could also just be more aware of their own work. The question of whether self-citations are justified is a key question and one that I’ve tried to address in an updated discussion.

Reviewer #3 (Recommendations for the Authors):

Data and code availablility are in good shape. At a high level, I recommend:

Toning down the interpretation of reviewers' motivation, especially since some of this is mitigated by findings presented in the paper.

I have reworded the discussion and included a warning on the observational study design.

Devote more time detailing exactly what data are being presented in each figure/table and results section as described in more detail in the main review (n, selection criteria, conditional subsetting, etc.).

I agree and have provided more details in each figure legend.

Reviewer #4 (Recommendations for the Authors):

A few aspects of the paper are not clear:

I did not follow Figure 4. Are the "self citation" labels supposed to be "citation to other research"?

Thanks for picking up this error which has now been fixed.

I did not understand how to parse the left column of Figure 2

As per the editor’s suggestion, the figure legend has been updated.

Table 3: Please use different markers for the different curves so that it is clearly demarcated even in grayscale print

I presume you meant Figure 3 not Table 3. I’ve varied the symbols in all three odds ratio plots.

Supplementary S3: Typo "Approvep" Fixed, thanks.

OTHER CHANGES: As well as the four reviews, my paper was reviewed by an AI-reviewer which provided some useful suggestions. I have mentioned this review in the acknowledgements. I have reversed the order of figure 5 to show the probability of “Approved” as this is simpler to interpret.

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

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Reply to the reviewers

We thank the reviewers for their detailed comments, which have already helped us improve our manuscript. The responses below detail changes we have already made as part of the Review Commons revision plan, and further changes we expect to make in a longer revision period.

__Reviewer #1 __

Major points __ It is mentioned throughout the manuscript that 3 plates were evaluated per line. I believe these are independently differentiated plates. This detail is critical concerning rigor and reproducibility. This should be clearly stated in the Methods section and in the first description of the experimental system in the Results section for Figure 1.__

These experimental details have now been clarified. Unless otherwise stated, all findings were confirmed in three independently differentiated plates from the same line or at least one differentiation from each of three lines.

For the patient-specific lines - how many lines were derived per patient?

This has now been clarified in the methods. Microfluidic reprogramming of a small number of amniocytes produces one line per patient representing a pool of clones. Subcloning from individual cells would not be possible within the timeframe of a pregnancy.

Methods: For patient-specific iPSC lines, one independent iPSC line was obtained per patient following microfluidic mmRNA reprogramming.

Was the Vangl2 variant introduced by prime editing? Base editing? The details of the methods are sparse.

We have now expanded these details:

Methods: VANGL2 knock-in lines were generated using CRSIPR-Cas9 homology directed repair editing by Synthego (SO-9291367-1). The guide sequence was AUGAGCGAAGGGUGCGCAAG and the donor sequence was CAATGAGTACTACTATGAGGAGGCTGAGCATGAGCGA AGGGTGTGCAAGAGGAGGGCCAGGTGGGTCCCTGGGGGAGAAGAGGAGAG. Sequence modification was confirmed by Sanger sequencing before delivery of the modified clones, and Sanger sequencing was repeated after expansion of the lines (Supplementary Figure 5) as well as SNP arrays (Illumina iScan, not shown) confirming genomic stability.

Some additional suggestions for improvement. __ The abstract could be more clearly written to effectively convey the study's importance. Here are some suggestions.__

Line 26: Insert "apicobasal" before "elongation" - the way it is written, I initially interpreted it as anterior-posterior elongation.

Line 29: Please specify that the lines refer to 3 different established parent iPSC lines with distinct origins and established using different reprogramming methods, plus 2 control patient-derived lines. - The reproducibility of the cell behaviors is impressive, but this is not captured in the abstract.

Line 32: add that this mutation was introduced by CRISPR-Cas9 base/prime editing.

The last sentence of the abstract states that the study only links apical constriction to human NTDs, but also reveals that neural differentiation and apical-basal elongation were found. __ The introduction could also use some editing. __ Line 71: insert "that pulls actin filaments together" after "power strokes" __ Line 73: "apically localized," do you mean "mediolaterally" or "radially"? __ Line 75: Can you specify that PCP components promote "mediolaterally orientated" apical constriction __ Lines 127: Specify that NE functions include apical basal elongation and neurodifferentiation are disrupted in patient-derived models__

These text changes have all been made.

Reviewer #2:____ __ __Major comments: __ 1. Figure 1. The authors use F-actin to segment cell areas. Perhaps this could be done more accurately with ZO-1, as F-actin cables can cross the surface of a single cell. In any case, the authors need to show a measure of segmentation precision: segmented image vs. raw image plus a nuclear marker (DAPI, H2B-GFP), so we can check that the number of segmented cells matches the number of nuclei.__

We used ZO-1 to quantify apical areas of the VANGL2-konckin lines in Figure 3. Segmentation of neuroepithelial apical areas based on F-actin staining is commonplace in the field (e.g. Fig 9 of Bogart & Brooks 2025 as a recent example), and is generally robust because the cell junctions are much brighter than any apical fibres not associated with the apical cortex. However, we accept that at earlier stages of differentiation there may be more apical fibres when cells are cuboidal. We have therefore repeated our analysis of apical area using ZO-1 staining as suggested, shown in the new Supplementary Figure 1, analysing a more temporally-detailed time course in one iPSC line. This new analysis confirms our finding of lack of apical area change between days 2-4 of differentiation, then progressive reduction of apical area between days 4-8, further validating our system. Including nuclear images is not helpful because of the high nuclear index of pseudostratified epithelia (e.g. see Supplementary Figure 7) which means that nuclei overlap along the apicobasal axis. Individual nuclei cannot be related to their apical surface in projected images.

__2.Lines 156-166. The authors claim that changes in gene expression precede morphological changes. I am not convinced this is supported by their data. Fig. 1g (epithelial thickness) and Fig. 1k (PAX6 expression) seem to have similar dynamics. The authors can perform a cross-correlation between the two plots to see which Δt gives maximum correlation. If Δt __We are happy to do this analysis fully in revision. __Our initial analysis performing cross-correlation between apical area and CDH2 protein in one line shows the highest cross-correlation at Δt = -1, suggesting neuroepithelial CDH2 increases before apical area decreases. In contrast, the same analysis comparing apical area versus PAX6 shows Δt = 0, suggesting concurrence. This analysis will be expanded to include the other markers we quantified and the manuscript text amended accordingly. We are keen to undertake additional experiments to test whether these cells swap their key cadherins - CDH1 and CDH2 - before they begin to undergo morphological changes (see the response to Reviewer 3's minor comment 1 immediately below).

3. Figure 2d. The laser ablation experiment in the presence of ROCK inhibitor is clear, as I can easily see the cell outlines before and after the experiment. In the absence of ROCK inhibitor, the cell edges are blurry, and I am not convinced the outline that the authors drew is really the cell boundary. Perhaps the authors can try to ablate a larger cell patch so that the change in area is more defined.

The outlines on these images are not intended to show cell boundaries, but rather link landmarks visible at both timepoints to calculate cluster (not cell) change in area. This is as previously shown in Galea et al Nat Commun 2021 and Butler et al J Cell Sci 2019. We have now amended the visualisation of retraction in Figure 2 to make representation of differences between conditions more intuitive.

4. Figure 2d. Do the cells become thicker after recoil?

This is unlikely because the ablated surface remains in the focal plane. Unfortunately, we are unable to image perpendicularly to the direction of ablation to test whether their apical surface moves in Z even by a very small amount. This has now been clarified in the results:

Results: The ablated surface remained within the focal plane after ablation, indicating minimal movement along the apical-basal axis.

5. Figure 3. The authors mention their previous study in which they show that Vangl2 is not cell-autonomously required for neural closure. It will be interesting to study whether this also the case in the present human model by using mosaic cultures.

We agree with the reviewer that this is one of the exciting potential future applications of our model, which will first require us to generate stable fluorescently-tagged lines (to identify those cells which lack VANGL2). We will also need to extensively analyze controls to validate that mixing fluo-tagged and untagged lines does not alter the homogeneity of differentiation, or apical constriction, independently of VANGL2 deletion. As such, the reviewer is suggesting an altogether new project which carries considerable risk and will require us to secure dedicated funding to undertake.

6. Lines 403-415. The authors report poor neural induction and neuronal differentiation in GOSB2. As far as I understand, this phenotype does not represent the in vivo situation. Thus, it is not clear to what extent the in vitro 2D model describes the human patient.

The GOSB2 iPSC line we describe does represent the in vivo situation in Med24 knockout mouse embryos, but is clearly less severe because we are still able to detect MED24 protein expressed in this line. We do not have detailed clinical data of the patient from which this line was obtained to determine whether their neurological development is normal. However, it is well established that some individuals who have spina bifida also have abnormalities in supratentorial brain development. It is therefore likely that abnormalities in neuron differentiation/maturation are concomitant with spina bifida. Our findings in the GOSB2 line complement earlier studies which also identified deficiencies in the ability of patient-derived lines to form neurons, but were unable to functionally assess neuroepithelial cell behaviours we studied. This has now been clarified in the discussion:

Discussion: *Neuroepithelial cells of the GOSB2 line described here, which has partial loss of MED24, similarly produces a thinner neuroepithelium with larger apical areas. Although apical areas were not analysed in mouse models of Med24 deletion, these embryos also have shorter and non-pseudostratified neuroepithelium. *

Our GOSB2 line - which retains readily detectable MED24 protein - is clearly less severe than the mouse global knockout, and the clinical features of the patient from which this line was derived are milder than the phenotype of Med24 knockout embryos68. Mouse embryos lacking one of Med24's interaction partners in the mediator complex, Med1, also have thinner neuroepithelium and diminished neuronal differentiation but successfully close their neural tube85.

7.The experimental feat to derive cell lines from amniotic fluid and to perform experiments before birth is, in my view, heroic. However, I do not feel I learned much from the in vitro assays. There are many genetic changes that may cause the in vivo phenotype in the patient. The authors focus on MED24, but there is not enough convincing evidence that this is the key gene. I would like to suggest overexpression of MED24 as a rescue experiment, but I am not sure this is a single-gene phenotype. In addition, the fact that one patient line does not differentiate properly leads me to think that the patient lines do not strengthen the manuscript, and that perhaps additional clean mutations might contribute more.

We thank the reviewer for their praise of our personalised medicine approach and fully agree that neural tube defects are rarely monogenic. The patient lines we studied were not intended to provide mechanistic insight, but rather to demonstrate the future applicability of our approach to patient care. Our vision is that every patient referred for fetal surgery of spina bifida will have amniocytes (collected as part of routine cystocentesis required before surgery) reprogrammed and differentiated into neuroepithelial cells, then neural progenitors, to help stratify their post-natal care. One could also picture these cells becoming an autologous source for future cell-based therapies if they pass our reproducible analysis pipeline as functional quality control. This has now been clarified in the discussion:

Discussion____: The multi-genic nature of neural tube defect susceptibility, compounded by uncontrolled environmental risk factors (including maternal age and parity102), mean that patient-derived iPSC models are unlikely to provide mechanistic insight. They do provide personalised disease models which we anticipate will enable functional validation of genetic diagnoses for patients and their parents' recurrence risk in future pregnancies, and may eventually stratify patients' postnatal care. We also envision this model will enable quality control of patient-derived cells intended for future autologous cell replacement therapies, as is being developed in post-natal spinal cord injury103.

Minor comments: __ 1.Figure 1c. Text is cropped at the edge of the image.__

This image has been corrected.

Reviewer #2 (Significance (Required)): __ ...In addition, the model was unsuccessful in one of the two patient-derived lines, which limits generalizability and weakens claims of patient-specific predictive value.__

We disagree with the reviewer that "the model was unsuccessful in one of the two patient-derived lines". The GOSB1 line demonstrated deficiency of neuron differentiation independently of neuroepithelial biomechanical function, whereas the GOSB2 line showed earlier failure of neuroepithelial function. We also do not, at this stage, make patient-specific predictive claims: this will require longer-term matching of cell model findings with patient phenotypes over the next 5-10 years.

Reviewer #3: Major comments __ 1) One of my few concerns with this work is that the relative constriction of the apical surface with respect to the basal surface is not directly quantified for any of the experiments. This worry is slightly compounded by the 3D reconstructions Figure 1h, and the observation that overall cell volume is reduced and cell height increased simultaneously to area loss. Additionally, the net impact of apical constriction in tissues in vivo is to create local or global curvature change, but all the images in the paper suggest that the differentiated neural tissues are an uncurved monolayer even missing local buckles. I understand that these cells are grown on flat adherent surfaces limiting global curvature change, but is there evidence of localized buckling in the monolayer? While I believe-along with the authors-that their phenotypes are likely failures in apical constriction, I think they should work to strengthen this conclusion. I think the easiest way (and hopefully using data they already have) would be to directly compare apical area to basal area on a cell wise basis for some number of cells. Given the heterogeneity of cells, perhaps 30-50 cells per condition/line/mutant would be good? I am open to other approaches; this just seems like it may not require additional experiments.__

As the reviewer observes, our cultures cannot bend because they are adhered on a rigid surface. The apical and basal lengths of the cultures will therefore necessarily be roughly equal in length. Some inwards bending of the epithelium is expected at the edges of the dish, but these cannot be imaged. The live imaging we show in Figure 2 illustrates that, just as happens in vivo, apical constriction is asynchronous. This means not all cells will have 'bottle' shapes in the same culture. We now illustrate the evolution of these shapes in more detail in Supplementary Figure 1 (shown in point 2.1 above).

Additionally, the reviewer's comment motivated us to investigate local buckles in the apical surface of our cultures when their apical surfaces are dilated by ROCK inhibition. We hypothesised that the very straight apical surface in normal cultures is achieved by a balance of apical cell size and tension with pressure differences at the cell-liquid interface. Consistent with our expectation, the apical surface of ROCK-inhibited cultures becomes wrinkled (new Supplementary Figure 3). The VANGL2-KI lines do not develop this tortuous apical surface (as shown in Figure 3), which is to be expected given their modification is present throughout differentiation unlike the acute dilation caused by ROCK inhibition.

This new data complements our visualisation of apical constriction in live imaging, apical accumulation of phospho-myosin, and quantification of ROCK-dependent apical tension as independent lines of evidence that our cultures undergo apical constriction.

2) Another slight experimental concern I have regards the difference in laser ablation experiments detailed in Figure 3h-i from those of Figure 2d-e. It seems like WT recoil values in 3h-I are more variable and of a lower average than the earlier experiments and given that it appears significance is reached mainly by impact of the lower values, can the authors explain if this variability is expected to be due to heterogeneity in the tissue, i.e. some areas have higher local tension? If so, would that correspond with more local apical constriction?

There is no significant difference in recoil between the control lines in Figures 2 and 3, albeit the data in Figure 3 is more variable (necessitating more replicates: none were excluded). We also showed laser ablation recoil data in Supplementary Figure 10, in which we did identify a graphing error (now corrected, also no significant difference in recoil from the other control groups).

Minor comments __ 1) There seems to be a critical window at day 5 of the differentiation protocol, both in terms of cell morphology and the marker panel presented in Figure 1i. Do the authors have any data spanning the hours from day 5 to 6? If not, I don't think they need to generate any, but do I think this is a very interesting window worthy of further discussion for a couple of reasons. First, several studies of mouse neural tube closure have shown that various aspects of cell remodeling are temporally separable. For example, between Grego-Bessa et al 2016 and Brooks et al 2020 we can infer that apicobasal elongation rapidly increases starting at E8.5, whereas apical surface area reduction and constriction are apparent somewhat earlier at E8.0. I think it would be interesting to see if this separability is conserved in humans. Second, is there a sense of how the temporal correlation between the pluripotent and early neural fate marker data presented here corroborate or contradict the emerging set of temporally resolved RNA seq data sets of mouse development at equivalent early neural stages?__

Cell shape analysis between days 5 and 6 has now been added (see the response to point 2.1 below). As the reviewer predicted, this is a transition point when apical area begins to decrease and apicobasal elongation begins to increase.

We also thank the reviewer for this prompt to more closely compare our data to the previous mouse publications, which we have added to the discussion. The Grego-Bessa 2016 paper appears to show an increase in thickness between E7.75 and E8.5, but these are not statistically compared. Previous studies showed rapid apicobasal elongation during the period of neural fold elevation, when neuroepithelial cells apically constrict. This has now been added to the discussion:

Discussion In mice, neuroepithelial apicobasal thickness is spatially-patterned, with shorter cells at the midline under the influence of SHH signalling14,77,78. Apicobasal thickness of the cranial neural folds increases from ~25 µm at E7.75 to ~50 µm at E8.579: closely paralleling the elongation between days 2 and 8 of differentiation in our protocol. The rate of thickening is non-uniform, with the greatest increase occurring during elevation of the neural folds80, paralleled in our model by the rapid increase in thickness between days 4-6 as apical areas decrease. Elevation requires neuroepithelial apical constriction and these cells' apical area also decreases between E7.75 and E8.5 in mice79, but we and others have recently shown that this reduction is both region and sex-specific14,81. Specifically, apical constriction occurs in the lateral (future dorsal) neuroepithelium: this corresponds with the identity of the cells generated by the dual SMAD inhibition model we use56. More recently, Brooks et al82 showed that the rapid reduction in apical area from E8-E8.5 is associated with cadherin switching from CDH1 (E-cadherin) to CDH2 (N-cadherin). This is also directly paralleled in our human system, which shows low-level co-expression of CDH1 and CDH2 at day 4 of differentiation, immediately before apical area shrinks and apicobasal thickness increases.

Prompted by the in vivo data in Brooks et al (2025)82, we are keen to further explore the timing of CDH1/CDH2 switching versus apical constriction with new experimental data in revisions.

2) Can the authors elaborate a bit more on what is known regarding apicobasal thickening and pseudo-stratification and how their work fits into the current understanding in the discussion? This is a very interesting and less well studied mechanism critical to closure, which their model is well suited to directly address. I am thinking mainly of the Grego-Bessa at al., 2016 work on PTEN, though interestingly the work of Ohmura et al., 2012 on the NUAK kinases also shows reduced tissue thickening (and apical constriction) and I am sure I have missed others. Given that the authors identify MED24 as a likely candidate for the lack of apicobasal thickening in one of their patient derived lines, is there any evidence that it interacts with any of the known players?

We have now added further discussion on the mechanisms by which the neuroepithelium undergoes apicobasal elongation. Nuclear compaction is likely to be necessary to allow pseudostratification and apicobasal elongation. The reviewer's comment has led us to realise that diminished chromatin compaction is a potential outcome of MED24 down-regulation in our GOSB2 patient-derived line. Figure 4D suggests the nuclei of our MED24 deficient patient-derived line are less compacted than control equivalents and we propose to quantify nuclear volume in more detail to explore this possibility.

Additionally, we have already expanded our discussion as suggested by the reviewer:

Discussion: *Mechanistic separability of apical constriction and apicobasal elongation is consistent with biomechanical modelling of Xenopus neural tube closure showing that both are independently required for tissue bending61. Nonetheless, neuroepithelial apical constriction and apicobasal elongation are co-regulated in mouse models: for example, deletion of Nuak1/283, Cfl184, and Pten79 all produce shorter neuroepithelium with larger apical areas. Neuroepithelial cells of the GOSB2 line described here, which has partial loss of MED24, similarly produces a thinner neuroepithelium with larger apical areas. Although apical areas were not analysed in mouse models of Med24 deletion, these embryos also have shorter and non-pseudostratified neuroepithelium. *

Our GOSB2 line - which retains readily detectable MED24 protein - is clearly less severe than the mouse global knockout, and the clinical features of the patient from which this line was derived are milder than the phenotype of Med24 knockout embryos68. Mouse embryos lacking one of Med24's interaction partners in the mediator complex, Med1, also have thinner neuroepithelium and diminished neuronal differentiation but successfully close their neural tube85. As general regulators of polymerase activity, MED proteins have the potential to alter the timing or level of expression of many other genes, including those already known to influence pseudostratification or apicobasal elongation. MED depletion also causes redistribution of cohesion complexes86 which may impact chromatin compaction, reducing nuclear volume during differentiation.

3) Is there any indication that Vangl2 is weakly or locally planar polarized in this system? Figure 2F seems to suggest not, but Supplementary Figure 5 does show at least more supracellular cable like structures that may have some polarity. I ask because polarization seems to be one of the properties that differs along the anteroposterior axis of the neural plate, and I wonder if this offers some insight into the position along the axis that this system most closely models?

VANGL2 does not appear to be planar polarised in this system. This is similar to the mouse spinal neuroepithelium, in which apical VANGL2 is homogenous but F-actin is planar polarised (Galea et al Disease Models and Mechanisms 2018). We do observe local supracellular cable-like enrichments of F-actin in the apical surface of iPSC-derived neuroepithelial cells. _We propose to compare the length of F-actin cables and coherency of their orientation at the start and end of neuroepithelial differentiation, and in wild-type versus VANGL2-mutant epithelia._

4) I think some of the commentary on the strengths and limitations of the model found in the Results section should be collated and moved to the discussion in a single paragraph. For example ' This could also briefly touch on/compare to some of the other models utilizing hiPSCs (These are mentioned briefly in the intro, but this comparison could be elaborated on a bit after seeing all the great data in this work).

These changes have now been made:

__Discussion: __Some of these limitations, potentially including inclusion of environmental risk factors, can be addressed by using alternative iPSC-derived models93,94. For example, if patients have suspected causative mutations in genes specific to the surface (non-neural) ectoderm, such as GRHL2/3, 3D models described by Karzbrun et al49 or Huang et al95 may be informative. Characterisation of surface ectoderm behaviours in those models is currently lacking. These models are particularly useful for high-throughput screens of induced mutations95, but their reproducibility between cell lines, necessary to compare patient samples to non-congenic controls, remains to be validated. Spinal cell identities can be generated in human spinal cord organoids, although these have highly variable morphologies96,97. As such, each iPSC model presents limitations and opportunities, to which this study contributes a reductionist and highly reproducible system in which to quantitatively compare multiple neuroepithelial functions.

5) While the authors are generally good about labeling figures by the day post smad inhibition, in some figures it is not clear either from the images or the legend text. I believe this includes supplemental figures 2,5,6,8, and 10 (apologies if I simply missed it in one or more of them)

These have now been added.

6) The legend for Figure 2 refers to a panel that is not present and the remaining panel descriptions are off by a letter. I'm guessing this is a versioning error as the text itself seems largely correct, but it may be good to check for any other similar errors that snuck in

This has now been corrected.

7) The cell outlines in Figure 3d are a bit hard to see both in print and on the screen, perhaps increase the displayed intensity?

This has now been corrected.

8) The authors show a fascinating piece of data in Supplementary Figure 1, demonstrating that nuclear volume is halved by day 8. Do they have any indication if the DNA content remains constant (e.g., integrated DAPI density)? I suppose it must, and this is a minor point in the grand scheme, but this represents a significant nuclear remodeling and may impact the overall DNA accessibility.

We agree with the reviewer that the reduction in nuclear volume is important data both because it informs understanding of the reduction in total cell volume, and because it suggests active chromatin compaction during differentiation. Unfortunately, the thicker epithelium and superimposition of nuclei in the differentiated condition means the laser light path is substantially different, making direct comparisons of intensity uninterpretable. Additionally, the apical-most nuclei will mostly be in G2/M phase due to interkinetic nuclear migration. As such, the comparison of DAPI integrated density between epithelial morphologies would not be informative.

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Referee #3

Evidence, reproducibility and clarity

This manuscript by Ampartzidis et al., significantly extends the human induced pluripotent stem cell system originally characterized by the same group as a tool for examining cellular remodeling during differentiation stages consistent with those of human neural tube closure (Ampartzidis et al., 2023). Given that there are no direct ways to analyze cellular activity in human neural tube closure in vivo, this model represents an important platform for investigating neural tube defects which are a common and deleterious human developmental disease. Here, the authors carefully test whether this system is robust and reproducible when using hiPSC cells from different donors and pluripotency induction methods and find that despite all these variables the cellular remodeling programs that occur during early neural differentiation are statistically equivalent, suggesting that this system is a useful experimental substrate. Additionally, the carefully selected donor populations suggest these aspects of human neural tube closure are likely to be robust to sexual dimorphism and to reasonable levels of human genetic background variation, though more fully testing that proposition would require significant effort and be beyond the scope of the current work. Subsequent to this careful characterization, the authors next tested whether this system could be used to derive specific insights into cell remodeling during early neural differentiation. First, they used a reverse genetics approach to knock in a human point mutation in the critical regulator of planar cell polarity and apical constriction, Vangl2. Despite being identified in a patient, this R353C variant has not been directly functionally tested in a human system. The authors find that this variant, despite showing normal expression and phospho-regulation, leads to defects consistent with a failure in apical constriction, a key cell behavior required to drive curvature change during cranial closure. Finally, the authors test the utility of their hiPSC platform to understand human patient-specific defects by differentiating cells derived from two clinical spina bifida patients. The authors identify that one of these patients is likely to have a significant defect in fully establishing early proneural identity as well as defects in apicobasal thickening. While early remodeling occurs normally in the other patient, the authors observe significant defects in later neuronal induction and maturation. In addition, using whole exome sequencing the authors identify candidate variant loci that could underly these defects.

Major comments

1) One of my few concerns with this work is that the relative constriction of the apical surface with respect to the basal surface is not directly quantified for any of the experiments. This worry is slightly compounded by the 3D reconstructions Figure 1h, and the observation that overall cell volume is reduced and cell height increased simultaneously to area loss. Additionally, the net impact of apical constriction in tissues in vivo is to create local or global curvature change, but all the images in the paper suggest that the differentiated neural tissues are an uncurved monolayer even missing local buckles. I understand that these cells are grown on flat adherent surfaces limiting global curvature change, but is there evidence of localized buckling in the monolayer? While I believe-along with the authors-that their phenotypes are likely failures in apical constriction, I think they should work to strengthen this conclusion. I think the easiest way (and hopefully using data they already have) would be to directly compare apical area to basal area on a cell wise basis for some number of cells. Given the heterogeneity of cells, perhaps 30-50 cells per condition/line/mutant would be good? I am open to other approaches; this just seems like it may not require additional experiments.

2) Another slight experimental concern I have regards the difference in laser ablation experiments detailed in Figure 3h-i from those of Figure 2d-e. It seems like WT recoil values in 3h-I are more variable and of a lower average than the earlier experiments and given that it appears significance is reached mainly by impact of the lower values, can the authors explain if this variability is expected to be due to heterogeneity in the tissue, i.e. some areas have higher local tension? If so, would that correspond with more local apical constriction?

Minor comments

1) There seems to be a critical window at day 5 of the differentiation protocol, both in terms of cell morphology and the marker panel presented in Figure 1i. Do the authors have any data spanning the hours from day 5 to 6? If not, I don't think they need to generate any, but do I think this is a very interesting window worthy of further discussion for a couple of reasons. First, several studies of mouse neural tube closure have shown that various aspects of cell remodeling are temporally separable. For example, between Grego-Bessa et al 2016 and Brooks et al 2020 we can infer that apicobasal elongation rapidly increases starting at E8.5, whereas apical surface area reduction and constriction are apparent somewhat earlier at E8.0. I think it would be interesting to see if this separability is conserved in humans. Second, is there a sense of how the temporal correlation between the pluripotent and early neural fate marker data presented here corroborate or contradict the emerging set of temporally resolved RNA seq data sets of mouse development at equivalent early neural stages?

2) Can the authors elaborate a bit more on what is known regarding apicobasal thickening and pseudo-stratification and how their work fits into the current understanding in the discussion? This is a very interesting and less well studied mechanism critical to closure, which their model is well suited to directly address. I am thinking mainly of the Grego-Bessa at al., 2016 work on PTEN, though interestingly the work of Ohmura et al., 2012 on the NUAK kinases also shows reduced tissue thickening (and apical constriction) and I am sure I have missed others. Given that the authors identify MED24 as a likely candidate for the lack of apicobasal thickening in one of their patient derived lines, is there any evidence that it interacts with any of the known players?

3) Is there any indication that Vangl2 is weakly or locally planar polarized in this system? Figure 2F seems to suggest not, but Supplementary Figure 5 does show at least more supracellular cable like structures that may have some polarity. I ask because polarization seems to be one of the properties that differs along the anteroposterior axis of the neural plate, and I wonder if this offers some insight into the position along the axis that this system most closely models?

4) I think some of the commentary on the strengths and limitations of the model found in the Results section should be collated and moved to the discussion in a single paragraph. For example ' This could also briefly touch on/compare to some of the other models utilizing hiPSCs (These are mentioned briefly in the intro, but this comparison could be elaborated on a bit after seeing all the great data in this work).

5) While the authors are generally good about labeling figures by the day post smad inhibition, in some figures it is not clear either from the images or the legend text. I believe this includes supplemental figures 2,5,6,8, and 10 (apologies if I simply missed it in one or more of them)

6) The legend for Figure 2 refers to a panel that is not present and the remaining panel descriptions are off by a letter. I'm guessing this is a versioning error as the text itself seems largely correct, but it may be good to check for any other similar errors that snuck in

7) The cell outlines in Figure 3d are a bit hard to see both in print and on the screen, perhaps increase the displayed intensity?

8) The authors show a fascinating piece of data in Supplementary Figure 1, demonstrating that nuclear volume is halved by day 8. Do they have any indication if the DNA content remains constant (e.g., integrated DAPI density)? I suppose it must, and this is a minor point in the grand scheme, but this represents a significant nuclear remodeling and may impact the overall DNA accessibility.

Significance

Overall, I am enthusiastic about this work and believe it represents a significant step forward in the effort to establish precision medicine approaches for diagnoses of the patient-specific causative cellular defects underlying human neural tube closure defects. This work systematizes an important and novel tool to examine the cellular basis of neural tube defects. While other hiPSC models of neural tube closure capture some tissue level dynamics, which this model does not, they require complex microfluidic approaches and have limited accessibility to direct imaging of cell remodeling. Comparatively, the relative simplicity of the reported model and the work demonstrating its tractability as a patient-specific and reverse genetic platform make it unique and attractive. This work will be of interest to a broad cross section of basic scientists interested in the cellular basis of tissue remodeling and/or the early events of nervous system development as well as clinical scientists interested in modeling the consequences of patient specific human genetic deficits identified in neural tube defect pregnancies.

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Referee #2

Evidence, reproducibility and clarity

The authors' work focuses on studying cell morphological changes during differentiation of hPSCs into neural progenitors in a 2D monolayer setting. The authors use genetic mutations in VANGL2 and patient-derived iPSCs to show that (1) human phenotypes can be captured in the 2D differentiation assay, and (2) VANGL2 in humans is required for neural contraction, which is consistent with previous studies in animal models. The results are solid and convincing, the data are quantitative, and the manuscript is well written. The 2D model they present successfully addresses the questions posed in the manuscript. However, the broad impact of the model may be limited, as it does not contain NNE cells and does not exhibit tissue folding or tube closure, as seen in neural tube formation. Patient-derived lines are derived from amniotic fluid cells, and the experiments are performed before birth, which I find to be a remarkable achievement, showing the future of precision medicine.

Major comments:

1.Figure 1. The authors use F-actin to segment cell areas. Perhaps this could be done more accurately with ZO-1, as F-actin cables can cross the surface of a single cell. In any case, the authors need to show a measure of segmentation precision: segmented image vs. raw image plus a nuclear marker (DAPI, H2B-GFP), so we can check that the number of segmented cells matches the number of nuclei. 2.Lines 156-166. The authors claim that changes in gene expression precede morphological changes. I am not convinced this is supported by their data. Fig. 1g (epithelial thickness) and Fig. 1k (PAX6 expression) seem to have similar dynamics. The authors can perform a cross-correlation between the two plots to see which Δt gives maximum correlation. If Δt < 0, then it would suggest that gene expression precedes morphology, as they claim. Fig. 1j shows that NANOG drops before the morphological changes, but loss of NANOG is not specific to neural differentiation and therefore should not be related to the observed morphological changes. 3.Figure 2d. The laser ablation experiment in the presence of ROCK inhibitor is clear, as I can easily see the cell outlines before and after the experiment. In the absence of ROCK inhibitor, the cell edges are blurry, and I am not convinced the outline that the authors drew is really the cell boundary. Perhaps the authors can try to ablate a larger cell patch so that the change in area is more defined. 4.Figure 2d. Do the cells become thicker after recoil? 5.Figure 3. The authors mention their previous study in which they show that Vangl2 is not cell-autonomously required for neural closure. It will be interesting to study whether this also the case in the present human model by using mosaic cultures. 6.Lines 403-415. The authors report poor neural induction and neuronal differentiation in GOSB2. As far as I understand, this phenotype does not represent the in vivo situation. Thus, it is not clear to what extent the in vitro 2D model describes the human patient. 7.The experimental feat to derive cell lines from amniotic fluid and to perform experiments before birth is, in my view, heroic. However, I do not feel I learned much from the in vitro assays. There are many genetic changes that may cause the in vivo phenotype in the patient. The authors focus on MED24, but there is not enough convincing evidence that this is the key gene. I would like to suggest overexpression of MED24 as a rescue experiment, but I am not sure this is a single-gene phenotype. In addition, the fact that one patient line does not differentiate properly leads me to think that the patient lines do not strengthen the manuscript, and that perhaps additional clean mutations might contribute more.

Minor comments:

1.Figure 1c. Text is cropped at the edge of the image.

Significance

This study establishes a quantitative, reproducible 2D human iPSC-to-neural-progenitor platform for analyzing cell-shape dynamics during differentiation. Using VANGL2 mutations and patient-derived iPSCs, the work shows that (1) human phenotypes can be captured in a 2D differentiation assay and (2) VANGL2 is required for neural contraction (apical constriction), consistent with animal studies. The results are solid, the data are quantitative, and the manuscript is well written. Although the planar system lacks non-neural ectoderm and does not exhibit tissue folding or tube closure, it provides a tractable baseline for mechanistic dissection and genotype-phenotype mapping. The derivation of patient lines from amniotic fluid and execution of experiments before birth is a remarkable demonstration that points toward precision-medicine applications, while motivating rescue strategies and additional clean genetic models. However, overall I did not learn anything substantively new from this manuscript; the conclusions largely corroborate prior observations rather than extend them. In addition, the model was unsuccessful in one of the two patient-derived lines, which limits generalizability and weakens claims of patient-specific predictive value.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Recommendations for the authors):

I think the authors did a fantastic job investigating the annotation issues I brought up in the first round. I am somewhat assured that the size of the dataset has prevented any real systematic issues from impacting their results. However, there are many clear underlying biases in the data, as the authors show, which could have a number of unexpected impacts on the results. For example, the consistently lower gene numbers could be biased towards certain types of genes or in certain lineages, making the CAZyme analysis unreliable. I do not agree with the author's choice to put these results in as a supplement with little or no other references to it in the main manuscript. Many of the conclusions that are drawn should be hedged by these findings. There should at least be a rational given for why the authors took the approach they did, such as mentioning the points they brought up in the response.

We thank the reviewer for the positive assessment of our revision. We added text in the Discussion acknowledging limitations of the gene annotation approach. 

“Because of the uniform yet simplified gene annotation approach, the total number of genes may be underestimated in some assemblies in our dataset, as observed when comparing the same species in JGI Mycocosm. Although this pattern is not biased toward any particular group of species, access to high-quality, well-annotated genomes could provide a clearer picture of the relative contributions of specific gene families.”

We also added more text in the Methods (section "Sordariomycetes genomes") mentioning in more detail the investigation of potential biases related to assembly quality and annotation (with reference to Supplementary Results).

A couple minor corrections:

Figure 1C, both axes say PC1?

Fixed.

Figure S12, scales don't match so it's hard to compare, axis labels are inconsistent.

Fixed.

Reviewer #2 (Recommendations for the authors):

I congratulate the authors on the revision work. Their manuscript is very interesting and reads very well.

I found several occurrences of « saprophyte ». Note that « saprotoph » is much better since fungi are not « phytes ».

We thank the reviewer for positive feedback. The occurrences of “saprophytes” were corrected.

Author response:

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

Reviewer #1 (Public review):

Summary:

van der Linden et al. report on the development of a new green-fluorescent sensor for calcium, following a novel rational design strategy based on the modification of the cyan-emissive sensor mTq2-CaFLITS. Through a mutational strategy similar to the one used to convert EGFP into EYFP, coupled with optimization of strategic amino acids located in proximity of the chromophore, they identify a novel sensor, GCaFLITS. Through a careful characterization of the photophysical properties in vitro and the expression level in cell cultures, the authors demonstrate that G-CaFLITS combines a large lifetime response with a good brightness in both the bound and unbound states. This relative independence of the brightness on calcium binding, compared with existing sensors that often feature at least one very dim form, is an interesting feature of this new type of sensors, which allows for a more robust usage in fluorescence lifetime imaging. Furthermore, the authors evaluate the performance of G-CaFLITS in different subcellular compartments and under two-photon excitation in Drosophila. While the data appears robust and the characterization thorough, the interpretation of the results in some cases appears less solid, and alternative explanations cannot be excluded.

Strengths:

The approach is innovative and extends the excellent photophysical properties of the mTq2-based to more red-shifted variants. While the spectral shift might appear relatively minor, as the authors correctly point out, it has interesting practical implications, such as the possibility to perform FLIM imaging of calcium using widely available laser wavelengths, or to reduce background autofluorescence, which can be a significant problem in FLIM.

The screening was simple and rationally guided, demonstrating that, at least for this class of sensors, a careful choice of screening positions is an excellent strategy to obtain variants with large FLIM responses without the need of high-throughput screening.

The description of the methodologies is very complete and accurate, greatly facilitating the reproduction of the results by others, or the adoption of similar methods. This is particularly true for the description of the experimental conditions for optimal screening of sensor variants in lysed bacterial cultures.

The photophysical characterization is very thorough and complete, and the vast amount of data reported in the supporting information is a valuable reference for other researchers willing to attempt a similar sensor development strategy. Particularly well done is the characterization of the brightness in cells, and the comparison on multiple parameters with existing sensors.

Overall, G-CaFLITS displays excellent properties for a FLIM sensor: very large lifetime change, bright emission in both forms and independence from pH in the physiological range.

Weaknesses:

The paper demonstrates the application of G-CaFLITS in various cellular subcompartments without providing direct evidence that the sensor's response is not affected by the targeting. Showing at least that the lifetime values in the saturated state are similar in all compartments would improve the robustness of the claims.

In some cases, the interpretation of the results is not fully convincing, leaving alternative hypotheses as a possibility. This is particularly the case for the claim of the origin of the strongly reduced brightness of G-CaFLITS in Drosophila. The explanation of the intensity changes of G-CaFLITS also shows some inconsistency with the basic photophysical characterization.

While the claims generally appear robust, in some cases they are conveyed with a lack of precision. Several sentences in the introduction and discussion could be improved in this regard. Furthermore, the use of the signal-to-noise ratio as a means of comparison between sensors appears to be imprecise, since it is dependent on experimental conditions.

We thank the reviewer for a thorough evaluation and for suggestions to improve our manuscript. We are happy with the recognition of the strengths of this work. The list with weaknesses has several valid points which will be addressed in a point-by-point reply and a revision.

Reviewer #2 (Public review):

Summary:

Van der Linden et al. describe the addition of the T203Y mutation to their previously described fluorescence lifetime calcium sensor Tq-Ca-FLITS to shift the fluorescence to green emission. This mutation was previously described to similarly red-shift the emission of green and cyan FPs. Tq-Ca-FLITS_T203Y behaves as a green calcium sensor with opposite polarity compared with the original (lifetime goes down upon calcium binding instead of up). They then screen a library of variants at

two linker positions and identify a variant with slightly improved lifetime contrast (TqCa-FLITS_T203Y_V27A_N271D, named G-Ca-FLITS). The authors then characterize the performance of G-Ca-FLITS relative to Tq-Ca-FLITS in purified protein samples, in cultured cells, and in the brains of fruit flies.

Strengths:

This work is interesting as it extends their prior work generating a calcium indicator scaffold for fluorescent protein-based lifetime sensors with large contrast at a single wavelength, which is already being adopted by the community for production of other FLIM biosensors. This work effectively extends that from cyan to green fluorescence. While the cyan and green sensors are not spectrally distinct enough (~20-30nm shift) to easily multiplex together, it at least shifts the spectra to wavelengths that are more commonly available on commercial microscopes.

The observations of organellar calcium concentrations were interesting and could potentially lead to new biological insight if followed up.

Weaknesses:

(1) The new G-Ca-FLITS sensor doesn't appear to be significantly improved in performance over the original Tq-Ca-FLITS, no specific benefits are demonstrated.

(2) Although it was admirable to attempt in vivo demonstration in Drosophila with these sensors, depolarizing the whole brain with high potassium is not a terribly interesting or physiological stimulus and doesn't really highlight any advantages of their sensors; G-Ca-FLITS appears to be quite dim in the flies.

We thank the reviewer for a thorough evaluation and for suggestions to improve our manuscript. Although the spectral shift of the green variant is modest, we have added new data (figure 7) to the manuscript that demonstrates multiplex imaging of G-Ca-FLITS and Tq-Ca-FLITS.

As for the listed weaknesses we respond here:

(1) Although we agree that the performance in terms of dynamic range is not improved, the advantage of the green sensor over the cyan version is that the brightness is high in both states.

(2) We agree that the performance of G-Ca-FLITS is disappointing in Drosophila. We feel that this is important data to report, and it makes it clear that Tq-Ca-FLITS is a better choice for this system. Depolarization of the entire brain was done to measure the maximal lifetime contrast.

Reviewer #3 (Public review):

Summary:

The authours present a variant of a previously described fluorescence lifetime sensor for calcium. Much of the manuscript describes the process of developing appropriate assays for screening sensor variants, and thorough characterization of those variants (inherent fluorescence characteristics, response to calcium and pH, comparisons to other calcium sensors). The final two figures show how the sensor performs in cultured cells and in vivo drosophila brains.

Strengths:

The work is presented clearly and the conclusion (this is a new calcium sensor that could be useful in some circumstances) is supported by the data.

Weaknesses:

There are probably few circumstances where this sensor would facilitate experiments (calcium measurements) that other sensors would prove insufficient.

We thank the reviewer for the evaluation of our manuscript. As for the indicated weakness, we agree that the main application of genetically encoded calcium biosensors is to measure qualitative changes in calcium. However, it can be argued that due to a lack of tools the absolute quantification has been very challenging. Now, thanks to large contrast lifetime biosensors the quantitative measurements are simplified, there are new opportunities, and the probe reported here is an improvement over existing probes as it remains bright in both states, further improving quantitative calcium measurements.

Reviewer #1 (Recommendations for the authors):

While the science in the paper appears solid, the methods well grounded and excellently documented, the manuscript would benefit from a revision to improve the clarity of the exposition. In particular:

Part of the introduction appears like a patchwork of information with poor logical consequentiality. The authors rapidly pass from the impact of brightness on FLIM accuracy, to mitochondrial calcium in pathology, to the importance of the sensor's affinity, to a sentence on sensor's kinetics, to fluorescent dyes and bioluminescence, to conclude that sensors should be stable at mitochondrial pH. I highly recommend rewriting this part.

We thank the referee for the comment and we have adjusted to introduction to better connect the parts and increase the logic. The updated introduction addresses all the feedback by the reviewers on different aspects of the introductory text, and we have removed the section on dyes and bioluminescence. We feel that the introduction is better structured now.

The reference to particular amino acid positions would greatly benefit from including images of the protein structure in which the positions are highlighted, similar to what the same authors do in their fluorescent protein development papers. While in the case of sensors a crystal structure might be lacking, highlighting the positions with respect to an AlphaFold-generated structure or the structure of mTq2 might still be helpful.

We appreciate this remark and we have added a sequence alignment of the FLITS probes to supplemental Figure S4. This shows the residues with number, and we have also highlighted the different domains, linkers and mutations. We think that this linear representation works better than a 3D structure (one issue is that alphafold fails to display the chromophore and it has usually poor confidence for linker residues).

The use of SNR, as defined by the authors (mean of the lifetime divided by standard deviation) appears a poorly suited parameter to compare sensors, as it depends on the total number of collected photons and on the strength of the algorithms used to retrieve the lifetime value. In an extreme example, if one would collect uniform images with millions of photons per pixel, most likely SNR would be extremely good for all sensors in all states, irrespective of the fact that some states are dimmer (within reasonable limits). On the other hand, if the same comparison would be performed at a level of thousands or hundreds of photons per pixel, the effect of different brightness on the SNR would be much more dramatic. While in general I fully agree with the core concept of the paper, i.e. that avoiding low-brightness forms leads more easily to experiments with higher SNR, I would suggest to stick to comparing the sensors in terms of brightness and refer to SNR (if needed) only when describing the consequences on measurements.

The reviewer is right that in absolute terms the SNR is not meaningful. In addition to acquisition time, it depends on expression levels. Yet, it is possible to compare the change in SNR between the apo- and saturated states, and that is what is shown in figure 5. We have added text to better explain that the change in SNR is relevant here:

“The absolute SNR is not relevant here, as it will depend on the expression level and acquisition time. But since we have measured the two extremes in the same cells, we can evaluate how the SNR changes between these states for each separate probe”

Some statements from the authors or aspects of the paper appear problematic:

(1) "Additionally, the fluorescence of most sensors is a non-linear function of calcium concentration, usually with Hill coefficients between 2 and 3. This is ideal when the probe is used as a binary detector for increases in Ca2+ concentrations, but it makes robust quantification of low, or even intermediate, calcium concentrations extremely challenging."

To the best of my knowledge, for all sensors the fluorescence response is a nonlinear function of calcium concentrations. If the authors have specific examples in mind in which this is not true, they should cite them specifically. Furthermore, the Hill coefficient defines the range of concentrations in which the sensor operates, while the fact that "low concentrations" might be hard to detect depends only on the dim fluorescence of some sensors in the unbound form.

We agree with the reviewer that this part is not clearly written and confusing, as the sentence “Additionally, the fluorescence of most sensors is a non-linear function of calcium concentration, usually with Hill coefficients between 2 and 3” was not relevant in this section and so we removed it. Now it reads:

“Many GECIs harboring a single fluorescent protein (FP), like GCaMPs, are optimized for a large intensity change, and have a (very) dim state when calcium levels are below the KD of the probe (Akerboom et al., 2013; Dana et al., 2019; Shen et al., 2018; Zhang et al., 2023; Zhao et al., 2011). This is ideal when the probe is used as a binary detector for increases in Ca2+ concentrations, but it makes robust quantification of low, or even intermediate, calcium concentrations extremely challenging”

(2) "The affinity of a sensor is of major importance: a low KD can underestimate high concentrations and vice versa."

It is not clear to me why the concentrations would be underestimated, rather than just being less precise. Also, if a calibration curve is plotted in linear scale rather than logarithmic scale, it appears that the precision problem is much more severe near saturation (where low lifetime changes result in large concentration changes) than near zero (where low concentration changes produce large lifetime changes).

We agree that this could be better explained, what we meant to say that concentrations that are ~10x lower or higher than the KD cannot be precisely measured. See also our reply to the next comment.

(3) "Differences can also arise due to the method of calibration, i.e. when the absolute minimum and maximum signal are not reached in the calibration procedure (Fernandez-Sanz et al., 2019)."

Unless better explained, this appears obvious and not worth mentioning.

What may be obvious to the reviewer (and to us) may not be obvious to the reader, and that’s why this is included. To make it clearer we rephrased this part as a list of four items:

“Accurate determination of the affinity of a sensor is important and there are several issues that need to be considered during the calibration and the measurements: (i) the concentrations can only be measured with sufficient precision when it is in the range between 10x K_D and 1/10x K_D, (ii) the calibration is only valid when the two extremes are reached during the calibration procedure (Fernandez-Sanz et al., 2019), (iii) the sensor’s kinetics should be sufficiently fast enough to be able to track the calcium changes, and (iv) the biosensor should be compatible with the high mitochondrial pH of 8 (Cano Abad et al., 2004; Llopis et al., 1998).”

(4) In the experiments depicted in Figure 6C the underlying assumption is that the sensor behaves in the same way independently of the compartment to which it is targeted. This is not necessarily the case. It would be valuable to see the plots of Figure 6C and D discussed in terms of lifetime. Is the saturating lifetime value the same in all compartments?

This is a valid point and we have now included a plot with the actual lifetime data for each of the organelles (figure S15). 

We have also added text to discuss this point: “We note that the underlying assumption of the quantification of organellar calcium concentrations is that the lifetime contrast is the same. This is broadly true for most of the measurements (Figure S15). Yet, there are also differences. It is currently unclear whether the discrepancies are due to differences in the physicochemical properties of the compartments, or whether there is a technical reason (the efficiency of ionomycin for saturating the biosensor in the different compartments is unknown, as far as we know). This is something that is worth revisiting. A related issue that deserves attention is the level of agreement between in vitro and in vivo calibrations.”

(5) A similar problem arises for the observation of different calcium levels in peripheral mitochondria. In figure S11b, the values of the two lifetime components of a biexponential fit are displayed. Both the long and short components seem to be different. This is an interesting observation, as in an ideal sensor (in which the "long lifetime conformation" is the same whether the sensor is bound to the analyte or not, and similarly for the short lifetime one) those values should be identical. While it is entirely possible that this is not the case for G-CaFLITS, since the authors have conducted a calibration experiment using time-domain FLIM, could they show the behavior of the lifetimes and preamplitudes? Are the trends consistent with their interpretation of a different calcium level in the two mitochondrial populations?

We have analyzed the calibration data from TCSPC experiments done with the Leica Stellaris. From these data (acquired at high photon counts as it is purified protein in solution), we infer that both the short and long lifetime do change as a function of calcium concentration. In particular the long lifetime shows a substantial change, which we cannot explain at this moment. We agree that this is interesting and may potentially give insight in the conformation changes that give rise to the lifetime change.

The lifetime data of the mitochondria has been acquired with a different FLIM setup, but the trend is consistent, both the long and short lifetime decrease in the peripheral mitochondria that have a higher calcium concentration.

Author response image 1

(6) "The lifetime response of Tq-Ca-FLITS and the ΔF/F response of jGCaMP7f resembled each other, with both signals gradually increasing over the span of 3-4 minutes after we increased external [K+]; the two signals then hit a plateau for ~1 min, followed by a return to baseline and often additional plateaus (Figure 8B-C). By comparison, G-Ca-FLITS responses were more variable, typically exhibiting a smaller ramping phase and seconds-long spikes of activity rather than minutes-long plateaus (Figure 8C)."

This statement does not appear fully consistent with the data in Figure 8. While in figure 8B it looks like GCaMP and mTq-CaFLITS have very similar profiles, these curves come from one single experiment out of a very variable dataset (see Figure 8C). If one would for example choose the second curve of GCaMP in Figure 8C, it would look very similar to the response of G-CaFLITS in figure 8B, and the argument would be reversed. How do the averages look like?

Indeed, the dynamics of the responses are very variable and we do not want to draw attention to these differences in the dynamics, so we have removed the comparison. Instead, the difference in intensity change and lifetime contrast are of importance here. To answer the question of the reviewer, we have added a new panel (D) which shows the average responses for each of the GECIs.  

(7) "Although the calibration is equipment independent under ideal conditions, and only needs to be performed once, we prefer to repeat the calibration for different setups to account for differences in temperature or pulse frequency."

While I generally agree with the statement, it is imprecise. A change in temperature is generally expected to affect the Kd, so rather than "preferring to repeat", it is a requirement for accurate quantification at different concentrations. I am not sure I understand what the pulse frequency is in this context, and how it affects the Kd.

We thank the referee for pointing out that our text is imprecise and confusing. What we meant to say is that we see differences between different set-ups and we have clarified this by changing the text. We have also added that it is “necessary” to repeat the calibration:

“Although the calibration is equipment independent under ideal conditions, and only needs to be performed once, we do see differences between different set-ups. Therefore, it is necessary to repeat the calibration for different set-ups.”

(8) "A recent effort to generate a green emitting lifetime biosensor used a GFP variant as a template (Koveal et al., 2022), and the resulting biosensor was pH sensitive in the physiological range. On the other hand, biosensors with a CFP-like chromophore are largely pH insensitive (van der Linden et al., 2021; Zhong et al., 2024)."

The dismissal of the use of T-Sapphire as a pH independent template is inaccurate. The same group has previously reported other sensors (SweetieTS for glucose and Peredox for redox ratio) that are not pH sensitive. Furthermore, in Koveal et al. also many of the mTq2-based variants showed a pH response, suggesting that the pHdependence for the Lilac sensor might be more complex. Still, G-CaFLITS present advantages in terms of the possibility to excite at longer wavelengths, which could be mentioned instead.

We only want to make the point that adding the T203Y mutation to Turquoise-based lifetime biosensors may be a good approach for generating pH insensitive green biosensors. There is no point in dismissing other green biosensors and we have changed the text to: “Since biosensors with a CFP-like chromophore are largely pH insensitive (van der Linden et al., 2021; Zhong et al., 2024), and we show here that the pH independence is retained for the Green Ca-FLITS, we expect that adding the T203Y mutation to a cyan sensor is a good approach for generating pH-insensitive green lifetime-based sensors.”

(9) "Usually, a higher QY results in a higher intensity; however, in G-Ca-FLITS the open state has a differential shaped excitation spectrum which leads to a decreased intensity. These effects combined have resulted in a sensor where the two different states have a similar intensity despite displaying a large QY and lifetime contrast."

This statement does not seem to reflect the excitation spectra of Figure 1. If this explanation would be true, wouldn't there be an isoemissive point in the excitation spectrum (i.e. an excitation wavelength at which emission intensity would not change)?

The excitation spectra in figure 1 are not ideal for the interpretation as these are not normalized. The normalized spectra are shown in figure S10, but for clarity we show the normalized spectra here below as well. For the FD-FLIM experiments we used a 446 nm LED that excites the calcium bound state more efficiently. Therefore, the lower brightness due to a lower QY of the calcium bound state is compensated by increased excitation. So the limited change in intensity is excitation wavelength dependent. We have added a sentence to the discussion to stress this:

“The smallest intensity change is obtained when the calcium-bound state is preferably excited (i.e. near 450 nm) and the effect is less pronounced when the probe is excited near its peak at 474 nm”   

(10) "We evaluated the use of Tq-Ca-FLITS and G-Ca-FLITS for 2P-FLIM and observed a surprisingly low brightness of the green variant in an intact fly brain. This result is consistent with a study finding that red-shifted fluorescent-protein variants that are much brighter under one-photon excitation are, surprisingly, dimmer than their blue cousins in multi-photon microscopy (Molina et al., 2017). The responses of both probes were in line with their properties in single photon FLIM, but given the low brightness of G-Ca-FLITS under 2-photon excitation, the Tq-Ca-FLITS may be a better choice for 2P-FLIM experiments."

The differences appear strikingly high, and it seems improbable that a reduction in two-photon absorption coefficient might be the sole cause. How can the authors rule out a problem in expression (possibly organism-specific)?

The reviewers are correct that the changes in brightness between G-Ca-FLITS and Tq-Ca-FLITS may arise from changes in expression levels. It is difficult to calibrate for these changes explicitly without a stable reference fluorophore. However, both the G-Ca-FLITS and Tq-Ca-FLITS transgenic flies produced used the same plasmid backbone (the Janelia 20x-UAS-IVS plasmid), landed in the same insertion site (VK00005) of the same genetic background and were crossed to the same Janelia driver line (R60D05-Gal4), so at the level of the transcriptional machinery or genetic regulatory landscape the two lines are probably identical except for the few base pair differences between the G-Ca-FLITS and Tq-Ca-FLITS sequence. But the same level of transcription may not correspond to the same amount of stable protein in the ellipsoid body. So, we cannot rule out any organism-specific problems in expression. To examine the 2P excitation efficiency relative to 1P excitation efficiency, we have measured the fluorescence intensity of purified G-Ca-FLITS and Tq-Ca-FLITS on beads. See also response to reviewer 3 and supplemental figure S14

Suggestions

(1) The underlying assumption of any experiment using a biosensor is that the concentration of the biosensor should be roughly 2 orders of magnitude lower than the concentration of the analyte, otherwise the calibration equations do not hold. When measuring nM concentrations of calcium, this problem can be in principle very significant, as the concentration of the sensor in cells is likely in the low micromolar range. Calcium regulation by the cell should compensate for the problem, and the equations should hold. However, this might not hold true during experimental conditions that would disrupt this tight regulation. It might be a good thing to add a sentence to inform users about the limitations in interpreting calcium concentration data under such conditions.

Good point. We have added this to the discussion: “All calcium indicators also act as buffers, and this limits the accuracy of the absolute measurements, especially for the lower calcium concentrations (Rose et al., 2014), as the expression of the biosensor is usually in the low micromolar range.”

(2) Different methods of lifetime "averaging", such as intensity or amplitude-weighted lifetime in time domain FLIM or phase and modulation in frequency domain might lead to different Kd in the same calibration experiment. This is an underappreciated factor that might lead to errors by users. Since the authors conducted calibrations using both frequency and time-domain, it would be useful to mention this fact and maybe add a table in the Supporting Information with the minima, maxima and Kds calculated using different lifetime averaging methods.

To avoid biases due to fitting we prefer to use the phasor plot, this can be used for both frequency and time-domain methods and we added a sentence to the discussion to highlight this: “We prefer to use the phasor analysis (which can be used for both frequency- and time-domain FLIM), as it makes no assumptions about the underlying decay kinetics.”

(3) The origin of the redshift observed in G-CaFLITS is likely pi-stacking, similar to the EGFP-to-EYFP case. While previous studies suggest that for mTq2 based sensors a change in rigidity would lead to a change in the non-radiative rate, which would result in similar changes in quantum yield and (amplitude-weighted average) lifetime. If pi-stacking plays a role, there could be an additional change in the radiative rate (as suggested also by the change in absorption spectra). Could this play a role in the relation between brightness and lifetime in G-CaFLITS? Given the extensive data collected by the authors, it should be possible to comment on these mechanistical aspects, which would be useful to guide future design.

We do appreciate this suggestion, but we currently do not have the data to answer this question. The inverted response that we observe, solely due to the introduction of the tyrosine is puzzling. Perhaps introduction of the mutation that causes the redshift in other cyan probes will provide more insight.

Reviewer #2 (Recommendations for the authors):

Specific points:

The first section of Results is basically a description of how they chose the lysis conditions for screening in bacteria. I didn't see anything particularly novel or interesting about this, anyone working with protein expression in bacteria likely needs to optimize growth, lysis, purification, etc. This section should be moved to the Methods.

As reviewer 1 lists the thorough documentation of this approach as one of the strengths, we prefer to keep it like this. We see this section as method development, rather than purely a method. When this section would be moved to methods, it remains largely invisible and we think that’s a shame. Readers that are not interested can easily skip this section.

In the Results section Characterization of G-Ca-FLITS, the authors state "Here, the calcium affinity was KD = 339 nM, higher compared to the calibration at 37{degree sign}C. This is in line with the notion that binding strength generally increases with decreasing temperature." However, the opposite appears to be true - at 37C they measured a KD of 209 nM which would represent higher binding strength at higher temperature.

Thanks for catching this, we’ve made a mistake. We rephrase this to “higher compared to the calibration at 37 ˚C. This is unexpected as it not in line with the notion that binding strength generally increases with decreasing temperature.”

In Figure 8c, there should be a visual indicator showing the onset of application of high potassium, as there is in 8b.

This is a good suggestion; a grey box is added to indicates time when high K+ saline was perfused.

Reviewer #3 (Recommendations for the authors):

I think the science of the manuscript is sound and the presentation is logical and clear. I have some stylistic recommendations.

Supp Fig 1: The figure requires a bit of "eyeballing" to decide which conditions are best, and figuring out which spectra matched the final conditions took a little effort. Is there a way to quantify the fluorescence yield to better show why the one set of conditions was chosen? If it was subjective, then at least highlight the final conditions with a box around the spectra, making it a different colour, or something to make it stand out.

Thanks for the comment; we added a green box.

Supp Fig 3: Similar suggestion. Highlight the final variant that was carried forward (T203Y). The subtle differences in spectra are hard to discern when they are presented separately. How would it look if they were plotted all on one graph? Or if each mutant were presented as a point on a graph of Peak Em vs Peak Ex? Would T203Y be in the top right?

We have added a light blue box for reference to make the differences clearer.

Supp Fig 4 & Fig 1: Too much of the graph show the uninteresting tails of the spectra and condenses the interesting part. Plotting from 400 nm to 600 nm would be more informative.

We appreciate the suggestion but disagree. We prefer to show the spectra in its entirety, including the tails. The data will be available so other plots can be made by anyone.

Fig 3a: People who are not experts in lifetime analysis are probably not very familiar with the phase/modulation polar plot. There should be an additional sentence or two in the main text that _briefly_ describes the basis for making the polar plot and the transformation to the fractional saturation plot in 3B. I can't think of a good way to transform Eq 3 from Supp Info into a sentence, but that's what I think is needed to make this transformation clearer.

We appreciate the suggestion and feel that it is well explained here:

"The two extreme values (zero calcium and 39 μM free calcium) are located on different coordinates in the polar plot and all intermediate concentrations are located on a straight line between these two extremes. Based on the position in the polar plot, we determined the fraction of sensor in the calcium-bound state, while considering the intensity contribution of both states"  

Fig 4: The figure is great, and I love the comparison of different calcium sensors. But where is Tq-Ca-FLITS? I get that this is a figure of green calcium sensors, but it would be nice to see Tq-Ca-FLITS in there as well. The G-Ca-FLITS is compared to Tq-Ca-FLITS in Fig 5. Maybe I'm just missing why the bottom panel of Fig 5 cannot be replotted and included in Fig 4.

The point is that we compare all the data with identical filter sets, i.e. for green FPs.using these ex/em settings, the Tq probe would seriously underperform. Note that the data in fig. 5 is not normalized to a reference RFP and can therefore not be compared with data presented in figure 4.

Fig 6: The BOEC data could easily be moved to Supp Figs. It doesn't contribute much relevant info.

We are not keen of moving data to supplemental, as too often the supplemental data is ignored. Moreover, we think that the BOEC data is valuable (as BOEC are primary cells and therefore a good model of a healthy human cell) and deserves a place in the main manuscript.

2P FLIM / Fig 8 / Fig S4: The lack of brightness of G-Ca-FLITS in the 2P FLIM of fruit fly brain could have been predicted with a 2P cross section of the purified protein. If the equipment to perform such measurements is available, it could be incorporated into Fig S4.

Unfortunately, we do not have access to equipment that measures the 2P cross section. As an alternative, we compared the 2P excitation efficiency with 1P excitation efficiency. To this end, we have used beads that were loaded with purified G-Ca-FLITS or Tq-Ca-FLITS. We have evaluated the fluorescence intensity of the beads using 1P (460 nm) and 2P (920 nm) excitation. Although the absolute intensity cannot be compared (the G-Ca-FLITS beads have a lower protein concentration), we can compare the relative intensities when changing from 1P to 2P. The 2P excitation efficiency of G-Ca-FLITS is comparable (if not better) to that of Tq-Ca-FLITS. This excludes the option that the G-Ca-FLITS has poor 2P excitability. We will include this data as figure S12.

We also have added text to the results: “We evaluated the relative brightness of purified Tq-Ca-FLITS and G-Ca-FLITS on beads by either 1-Photon Excitation (1PE) (at 460 nm) or 2-Photon Excitation (2PE) (at 920 nm) and observed a similar brightness between the two modes of excitations (figure S14). This shows that the two probes have similar efficiencies in 2PE and suggest that the low brightness of GCa-FLITS in Drosophila is due to lower expression or poor folding.” and discussion: “The responses of both probes were in line with their properties in single photon FLIM, but given the low brightness of G-Ca-FLITS under 2-photon excitation in Drosphila, the Tq-Ca-FLITS is a better choice in this system. Yet, the brightness of G-Ca-FLITS with 2PE at 920 nm is comparable to Tq-Ca-FLITS, so we expect that 2P-FLIM with G-Ca-FLITS is possible in tissues that express it well.”

Author Response:

Reviewer #1 (Public Review):

The work by Wang et al. examined how task-irrelevant, high-order rhythmic context could rescue the attentional blink effect via reorganizing items into different temporal chunks, as well as the neural correlates. In a series of behavioral experiments with several controls, they demonstrated that the detection performance of T2 was higher when occurring in different chunks from T1, compared to when T1 and T2 were in the same chunk. In EEG recordings, they further revealed that the chunk-related entrainment was significantly correlated with the behavioral effect, and the alpha-band power for T2 and its coupling to the low-frequency oscillation were also related to behavioral effect. They propose that the rhythmic context implements a second-order temporal structure to the first-order regularities posited in dynamic attention theory.

Overall, I find the results interesting and convincing, particularly the behavioral part. The manuscript is clearly written and the methods are sound. My major concerns are about the neural part, i.e., whether the work provides new scientific insights to our understanding of dynamic attention and its neural underpinnings.

1) A general concern is whether the observed behavioral related neural index, e.g., alpha-band power, cross-frequency coupling, could be simply explained in terms of ERP response for T2. For example, when the ERP response for T2 is larger for between-chunk condition compared to within-chunk condition, the alpha-power for T2 would be also larger for between-chunk condition. Likewise, this might also explain the cross-frequency coupling results. The authors should do more control analyses to address the possibility, e.g., plotting the ERP response for the two conditions and regressing them out from the oscillatory index.

Many thanks for the comment. In short, the enhancement in alpha power and cross-frequency coupling results in the between-cycle condition compared with those in the within-cycle condition cannot be accounted for by the ERP responses for T2.

In general, the rhythmic stimulation in the AB paradigm prevents EEG signals from returning to the baseline. Therefore, we cannot observe typical ERP components purely related to individual items, except for the P1 and N1 components related to the stream onset, which reveals no difference between the two conditions and are trailed by steady-state responses (SSRs) resonating at the stimulus rate (Fig. R1).

Fig. R1. ERPs aligned to stream onset. EEG signals were filtered between 1–30 Hz, baseline-corrected (-200 to 0 ms before stream onset) and averaged across the electrodes in left parieto-occipital area where 10-Hz alpha power showed attentional modulation effect.

To further inspect the potential differences in the target-related ERP signals between the within- and between-cycle conditions, we plotted the target-aligned waveforms for these experimental conditions. As shown in Fig. R2, a drop of ERP amplitude occurred for both conditions around T2 onset, and the difference between these two conditions was not significant (paired t-test estimated on mean amplitude every 20 ms from 0 to 700 ms relative to T1 onset, p > .05, FDR-corrected).

Fig. R2. ERPs aligned to T1 onset. EEG signals were filtered between 1–30 Hz, and baseline-corrected using signals -100 to 0 ms before T1 onset. The two dash lines indicate the onset of T1 and T2, respectively.

Since there is a trend of enhanced ERP response for the between-cycle relative to the within-cycle condition during the period of 0 to 100 ms after T2 onset (paired t-test on mean amplitude, p =.065, uncorrected), we then directly examined whether such post-T2 responses contribute to the behavioral attentional modulation effect and behavior-related neural indices. Crucially, we did not find any significant correlation of such T2-related ERP enhancement with the behavioral modulation index (BMI), or with the reported effects of alpha power and cross-frequency coupling (PAC). Furthermore, after controlling for the T2-related ERP responses, there still remains a significant correlation between the delta-alpha PAC and the BMI (rpartial = .596, p = .019), which is not surprising given that the PAC is calculated based on an 800-ms time window covering more pre-T2 than post-T2 periods (see the response to point #4 for details) rather than around the T2 onset. Taken together, these results clearly suggest that the T2-related ERP responses cannot explain the attentional modulation effect and the observed behavior-related neural indices.

2) The alpha-band increase for T2 is indeed contradictory to the well known inhibitory function of alpha-band in attention. How could a target that is better discriminated elicit stronger inhibitory response? Related to the above point, the observed enhancement in alpha-band power and its coupling to low-frequency oscillation might derive from an enhanced ERP response for T2 target.

Many thanks for the comment. We have briefly discussed this point in the revised manuscript (page 18, line 477).

A widely accepted function of alpha activity in attention is that alpha oscillations suppress irrelevant visual information during spatial selection (Kelly et al., 2006; Thut et al., 2006; Worden et al., 2000). However, it becomes a controversial issue when there exists rhythmic sensory stimulation at alpha-band, just like the situation in the current study where both the visual stream and the contextual auditory rhythm were emitted at 10 Hz. In such a case, alpha-band neural responses at the stimulation frequency can be interpreted as either passively evoked steady-state responses (SSR) or actively synchronized intrinsic brain rhythms. From the former perspective (i.e., the SSR view), an increase in the amplitude or power at the stimulus frequency may indicate an enhanced attentional allocation to the stimulus stream that may result in better target detection (Janson et al., 2014; Keil et al., 2006; Müller & Hübner, 2002). Conversely, the latter view of the inhibitory function of intrinsic alpha oscillations would produce the opposite prediction. In a previous AB study, Janson and colleagues (2014) investigated this issue by separating the stimulus-evoked activity at 12 Hz (using the same power analysis method as ours) from the endogenous alpha oscillations ranging from 10.35 to 11.25 Hz (as indexed by individual alpha frequency, IAF). Interestingly, they found a dissociation between these two alpha-band neural responses, showing that the RSVP frequency power was higher in non-AB trials (T2 detected) than in AB trials (T2 undetected) while the IAF power exhibited the opposite pattern. According to these findings, the currently observed increase in alpha power for the between-cycle condition may reflect more of the stimulus-driven processes related to attentional enhancement. However, we don’t negate the effect of intrinsic alpha oscillations in our study, as the current design is not sufficient to distinguish between these two processes. We have discussed this point in the revised manuscript (page 18, line 477). Also, we have to admit that “alpha power” may not be the most precise term to describe our findings of the stimulus-related results. Thus, we have specified it as “neural responses to first-order rhythms at 10 Hz” and “10-Hz alpha power” in the revised manuscript (see page 12 in the Results section and page 18 in the Discussion section).

As for the contribution of T2-related ERP response to the observed effect of 10 Hz power and cross-frequency coupling, please refer to our response to point #1.

References:

Janson, J., De Vos, M., Thorne, J. D., & Kranczioch, C. (2014). Endogenous and Rapid Serial Visual Presentation-induced Alpha Band Oscillations in the Attentional Blink. Journal of Cognitive Neuroscience, 26(7), 1454–1468. https://doi.org/10.1162/jocn_a_00551

Keil, A., Ihssen, N., & Heim, S. (2006). Early cortical facilitation for emotionally arousing targets during the attentional blink. BMC Biology, 4(1), 23. https://doi.org/10.1186/1741-7007-4-23

Kelly, S. P., Lalor, E. C., Reilly, R. B., & Foxe, J. J. (2006). Increases in Alpha Oscillatory Power Reflect an Active Retinotopic Mechanism for Distracter Suppression During Sustained Visuospatial Attention. Journal of Neurophysiology, 95(6), 3844–3851. https://doi.org/10.1152/jn.01234.2005

Müller, M. M., & Hübner, R. (2002). Can the Spotlight of Attention Be Shaped Like a Doughnut? Evidence From Steady-State Visual Evoked Potentials. Psychological Science, 13(2), 119–124. https://doi.org/10.1111/1467-9280.00422

Thut, G., Nietzel, A., Brandt, S., & Pascual-Leone, A. (2006). Alpha-band electroencephalographic activity over occipital cortex indexes visuospatial attention bias and predicts visual target detection. The Journal of Neuroscience : The Official Journal of the Society for Neuroscience, 26(37), 9494–9502. https://doi.org/10.1523/JNEUROSCI.0875-06.2006

Worden, M. S., Foxe, J. J., Wang, N., & Simpson, G. V. (2000). Anticipatory Biasing of Visuospatial Attention Indexed by Retinotopically Specific α-Bank Electroencephalography Increases over Occipital Cortex. Journal of Neuroscience, 20(6), RC63–RC63. https://doi.org/10.1523/JNEUROSCI.20-06-j0002.2000

3) To support that it is the context-induced entrainment that leads to the modulation in AB effect, the authors could examine pre-T2 response, e.g., alpha-power, and cross-frequency coupling, as well as its relationship to behavioral performance. I think the pre-stimulus response might be more convincing to support the authors' claim.

Many thanks for the insightful suggestion. We have conducted additional analyses.

Following this suggestion, we have examined the 10-Hz alpha power within the time window of -100–0 ms before T2 onset and found stronger activity for the between-cycle condition than for the within-cycle condition. This pre-T2 response is similar to the post-T2 response except that it is more restricted to the left parieto-occipital cluster (CP3, CP5, P3, P5, PO3, PO5, POZ, O1, OZ, t(15) = 2.774, p = .007), which partially overlaps with the cluster that exhibits a delta-alpha coupling effect significantly correlated with the BMI. We have incorporated these findings into the main text (page 12, line 315) and the Fig. 5A of the revised manuscript.

As for the coupling results reported in our manuscript, the coupling index (PAC) was calculated based on the activity during the second and third cycles (i.e., 400 to 1200 ms from stream onset) of the contextual rhythm, most of which covers the pre-T2 period as T2 always appeared in the third cycle for both conditions. Together, these results on pre-T2 10-Hz alpha power and cross-frequency coupling, as well as its relationship to behavioral performance, jointly suggest that the observed modulation effect is caused by the context-induced entrainment rather than being a by-product of post-T2 processing.

4) About the entrainment to rhythmic context and its relation to behavioral modulation index. Previous studies (e.g., Ding et al) have demonstrated the hierarchical temporal structure in speech signals, e.g., emergence of word-level entrainment introduced by language experience. Therefore, it is well expected that imposing a second-order structure on a visual stream would elicit the corresponding steady-state response. I understand that the new part and main focus here are the AB effects. The authors should add more texts explaining how their findings contribute new understandings to the neural mechanism for the intriguing phenomena.

Many thanks for the suggestion. We have provided more discussion in the revised manuscript (page 17, line 447).

We have provided more discussion on this important issue in the revised manuscript (page 17, line 447). In brief, our study demonstrates how cortical tracking of feature-based hierarchical structure reframes the deployment of attentional resources over visual streams. This effect, distinct from the hierarchical entrainment to speech signals (Ding et al., 2016; Gross et al., 2013), does not rely on previously acquired knowledge about the structured information and can be established automatically even when the higher-order structure comes from a task-irrelevant and cross-modal contextual rhythm. On the other hand, our finding sheds fresh light on the adaptive value of the structure-based entrainment effect by expanding its role from rhythmic information (e.g., speech) perception to temporal attention deployment. To our knowledge, few studies have tackled this issue in visual or speech processing.

References:

Ding, N., Melloni, L., Zhang, H., Tian, X., & Poeppel, D. (2016). Cortical tracking of hierarchical linguistic structures in connected speech. Nature Neuroscience, 19(1), 158–164. https://doi.org/10.1038/nn.4186

Gross, J., Hoogenboom, N., Thut, G., Schyns, P., Panzeri, S., Belin, P., & Garrod, S. (2013). Speech Rhythms and Multiplexed Oscillatory Sensory Coding in the Human Brain. PLoS Biol, 11(12). https://doi.org/10.1371/journal.pbio.1001752

Reviewer #2 (Public Review):

In cognitive neuroscience, a large number of studies proposed that neural entrainment, i.e., synchronization of neural activity and low-frequency external rhythms, is a key mechanism for temporal attention. In psychology and especially in vision, attentional blink is the most established paradigm to study temporal attention. Nevertheless, as far as I know, few studies try to link neural entrainment in the cognitive neuroscience literature with attentional blink in the psychology literature. The current study, however, bridges this gap.

The study provides new evidence for the dynamic attending theory using the attentional blink paradigm. Furthermore, it is shown that neural entrainment to the sensory rhythm, measured by EEG, is related to the attentional blink effect. The authors also show that event/chunk boundaries are not enough to modulate the attentional blink effect, and suggest that strict rhythmicity is required to modulate attention in time.

In general, I enjoyed reading the manuscript and only have a few relatively minor concerns.

1) Details about EEG analysis.

. First, each epoch is from -600 ms before the stimulus onset to 1600 ms after the stimulus onset. Therefore, the epoch is 2200 s in duration. However, zero-padding is needed to make the epoch duration 2000 s (for 0.5-Hz resolution). This is confusing. Furthermore, for a more conservative analysis, I recommend to also analyze the response between 400 ms and 1600 ms, to avoid the onset response, and show the results in a supplementary figure. The short duration reduces the frequency resolution but still allows seeing a 2.5-Hz response.

Thanks for the comments. Each epoch was indeed segmented from -600 to 1600 ms relative to the stimulus onset, but in the spectrum analysis, we only used EEG signals from stream onset (i.e., time point 0) to 1600 ms (see the Materials and Methods section) to investigate the oscillatory characteristics of the neural responses purely elicited by rhythmic stimuli. The 1.6-s signals were zero-padded into a 2-s duration to achieve a frequency resolution of 0.5 Hz.

According to the reviewer’s suggestion, we analyzed the EEG signals from 400 ms to 1600 ms relative to stream onset to avoid potential influence of the onset response, and showed the results in Figure 4. Basically, we can still observe spectral peaks at the stimulus frequencies of 2.5, 5 (the harmonic of 2.5 Hz), and 10 Hz for both power and ITPC spectrum. However, the peak magnitudes were much weaker than those of 1.6-s signals especially for 2.5 Hz, and the 2.5-Hz power did not survive the multiple comparisons correction across frequencies (FDR threshold of p < .05), which might be due to the relatively low signal-to-noise ratio for the analysis based on the 1.2-s epochs (only three cycles to estimate the activity at 2.5 Hz). Importantly, we did identify a significant cluster for 2.5 Hz ITPC in the left parieto-occipital region showing a positive correlation with the individuals’ BMI (Fig. R3; CP5, TP7, P5, P7, PO5, PO7, O1; r = .538, p = .016), which is consistent with the findings based on the longer epochs.

Fig. R3. Neural entrainment to contextual rhythms during the period of 400–1600 ms from stream onset. (A) The spectrum for inter-trial phase coherence (ITPC) of EEG signals from 400 to 1600 ms after the stimulus onset. Shaded areas indicate standard errors of the mean. (B) The 2.5-Hz ITPC was significantly correlated with the behavioral modulation index (BMI) in a parieto-occipital cluster, as indicated by orange stars in the scalp topographic map.

Second, "The preprocessed EEG signals were first corrected by subtracting the average activity of the entire stream for each epoch, and then averaged across trials for each condition, each participant, and each electrode." I have several concerns about this procedure.

(A) What is the entire stream? It's the average over time?

Yes, as for the power spectrum analysis, EEG signals were first demeaned by subtracting the average signals of the entire stream over time from onset to offset (i.e., from 0 to 1600 ms) before further analysis. We performed this procedure following previous studies on the entrainment to visual rhythms (Spaak et al., 2014). We have clarified this point in the “Power analysis” part of the Materials and Methods section (page 25, line 677).

References:

Spaak, E., Lange, F. P. de, & Jensen, O. (2014). Local Entrainment of Alpha Oscillations by Visual Stimuli Causes Cyclic Modulation of Perception. The Journal of Neuroscience, 34(10), 3536–3544. https://doi.org/10.1523/JNEUROSCI.4385-13.2014

(B) I suggest to do the Fourier transform first and average the spectrum over participants and electrodes. Averaging the EEG waveforms require the assumption that all electrodes/participants have the same response phase, which is not necessarily true.

Thanks for the suggestion. In an AB paradigm, the evoked neural responses are sufficiently time-locked to the periodic stimulation, so it is reasonable to quantify power estimate with spectral decomposition performed on trial-averaged EEG signals (i.e., evoked power). Moreover, our results of inter-trial phase coherence (ITPC), which estimated the phase-locking value across trials based on single-trial decomposed phase values, also provided supporting evidence that the EEG waveforms were temporally locked across trials to the 2.5-Hz temporal structure in the context session.

Nevertheless, we also took the reviewer’s suggestion seriously and analyzed the power spectrum on the average of single-trial spectral transforms, i.e., the induced power, which puts emphasis on the intrinsic non-phase-locked activities. In line with the results of evoked power and ITPC, the induced power spectrum in context session also peaked at 2.5 Hz and was significantly stronger than that in baseline session at 2.5 Hz (t(15) = 4.186, p < .001, FDR-corrected with a p value threshold < .001). Importantly, Person correlation analysis also revealed a positive cluster in the left parieto-occipital region, indicating the induced power at 2.5 Hz also had strong relevance with the attentional modulation effect (P7, PO7, PO5, PO3; r = .606, p = .006). We have added these additional findings to the revised manuscript (page 11, line 288; see also Figure 4—figure supplement 1).

2) The sequences are short, only containing 16 items and 4 cycles. Furthermore, the targets are presented in the 2nd or 3rd cycle. I suspect that a stronger effect may be observed if the sequence are longer, since attention may not well entrain to the external stimulus until a few cycles. In the first trial of the experiment, they participant may not have a chance to realize that the task-irrelevant auditory/visual stimulus has a cyclic nature and it is not likely that their attention will entrain to such cycles. As the experiment precedes, they learns that the stimulus is cyclic and may allocate their attention rhythmically. Therefore, I feel that the participants do not just rely on the rhythmic information within a trial but also rely on the stimulus history. Please discuss why short sequences are used and whether it is possible to see buildup of the effect over trials or over cycles within a trial.

Thanks for the comments. Typically, to induce a classic pattern of AB effect, the RSVP stream should contain 3–7 distractors before the first target (T1), with varying lengths of distractors (0–7) between two targets and at least 2 items after the second target (T2). In our study, we created the RSVP streams following these rules, which allowed us to observe the typical AB effect that T2 performance was deteriorated at Lag 2 relative to that at Lag 8. Nevertheless, we agree with the reviewer that longer streams would be better for building up the attentional entrainment effect, as we did observe the attentional modulation effect ramped up as the stream proceeded over cycles, consistent with the reviewer’s speculation. In Experiments 1a (using auditory context) and 2a (using color-defined visual context), we adopted two sets of target positions—an early one where T2 appeared at the 6th or 8th position (in the 2nd cycle) of the visual stream, and a late one where T2 appeared at the 10th or 12th position (in the 3rd cycle) of the visual stream. In the manuscript, we reported T2 performance with all the target positions combined, as no significant interaction was found between the target positions and the experimental conditions (ps. > .1). However, additional analysis demonstrated a trend toward an increase of the attentional modulation effect over cycles, from the early to the late positions. As shown in Fig. R4, the modulation effect went stronger and reached significance for the late positions (for Experiment 1a, t(15) = 2.83, p = .013, Cohen’s d = 0.707; for Experiment 2a, t(15) = 3.656, p = .002, Cohen’s d = 0.914) but showed a weaker trend for the early positions (for Experiment 1a, t(15) = 1.049, p = .311, Cohen’s d = 0.262; for Experiment 2a, t(15) = .606, p = .553, Cohen’s d = 0.152).

Fig. R4. Attentional modulation effect built up over cycles in Experiments 1a & 2a. Error bars represent 1 SEM; * p<0.05, ** p<0.01.

However, we did not observe an obvious buildup effect across trials in our study. The modulation effect of contextual rhythms seems to be a quick process that the effect is evident in the first quarter of trials in Experiment 1a (for, t(15) = 2.703, p = .016, Cohen’s d = 0.676) and in the second quarter of trials in Experiment 2a (for, t(15) = 2.478, p = .026, Cohen’s d = 0.620.

3) The term "cycle" is used without definition in Results. Please define and mention that it's an abstract term and does not require the stimulus to have "cycles".

Thanks for the suggestion. By its definition, the term “cycle” refers to “an interval of time during which a sequence of a recurring succession of events or phenomena is completed” or “a course or series of events or operations that recur regularly and usually lead back to the starting point” (Merriam-Webster dictionary). In the current study, we stuck to the recurrent and regular nature of “cycle” in general while defined the specific meaning of “cycle” by feature-based periodic changes of the contextual stimuli in each experiment (page 5, line 101; also refer to Procedures in the Materials and Methods section for details). For example, in Experiment 1a, the background tone sequence changed its pitch value from high to low or vice versa isochronously at a rate of 2.5 Hz, thus forming a rhythmic context with structure-based cycles of 400 ms. Note that we did not use the more general term “chunk”, because arbitrary chunks without the regularity of cycles are insufficient to trigger the attentional modulation effect in the current study. Indeed, the effect was eliminated when we replaced the rhythmic cycles with irregular chunks (Experiments 1d & 1e).

4) Entrainment of attention is not necessarily related to neural entrainment to sensory stimulus, and there is considerable debate about whether neural entrainment to sensory stimulus should be called entrainment. Too much emphasis on terminology is of course counterproductive but a short discussion on these issues is probably necessary.

Thanks for the comments. As commonly accepted, entrainment is defined as the alignment of intrinsic neuronal activity to the temporal structure of external rhythmic inputs (Lakatos et al., 2019; Obleser & Kayser, 2019). Here, we are interested in the functional roles of cortical entrainment to the higher-order temporal structure imposed on first-order sensory stimulation, and used the term entrainment to describe the phase-locking neural responses to such hierarchical structure following literature on auditory and visual perception (Brookshire et al., 2017; Doelling & Poeppel, 2015). In our study, the consistent results of power and ITPC have provided strong evidence that neural entrainment at the structure level (2.5 Hz) is significantly correlated with the observed attentional modulation effect. However, this does not mean that the entrainment of attention is necessarily associated with neural entrainment to sensory stimulus in a broader context, as attention may also be guided by predictions based on non-isochronous temporal regularity without requiring stimulus-based oscillatory entrainment (Breska & Deouell, 2017; Morillon et al._2016).

On the other hand, there has been a debate about whether the neural alignment to rhythmic stimulation reflects active entrainment of endogenous oscillatory processes (i.e., induced activity) or a series of passively evoked steady-state responses (Keitel et al., 2019; Notbohm et al., 2016; Zoefel et al., 2018). The latter process is also referred to as “entrainment in a broad sense” by Obleser & Kayser (2019). Given that a presented rhythm always evokes event-related potentials, a better question might be whether the observed alignment reflects the entrainment of endogenous oscillations in addition to evoked steady-state responses. Here we attempted to tackle this issue by measuring the induced power, which emphasizes the intrinsic non-phase-locked activity, in addition to the phase-locked evoked power. Specifically, we quantified these two kinds of activities with the average of single-trial EEG power spectra and the power spectra of trial-averaged EEG signals, respectively, according to Keitel et al. (2019). In addition to the observation of evoked responses to the contextual structure, we also demonstrated an attention-related neural tracking of the higher-order temporal structure based on the induced power at 2.5 Hz (see Figure 4—figure supplement 1), suggesting that the observed attentional modulation effect is at least partially derived from the entrainment of intrinsic oscillatory brain activity. We have briefly discussed this point in the revised manuscript (page 17, line 460).

References:

Breska, A., & Deouell, L. Y. (2017). Neural mechanisms of rhythm-based temporal prediction: Delta phase-locking reflects temporal predictability but not rhythmic entrainment. PLOS Biology, 15(2), e2001665. https://doi.org/10.1371/journal.pbio.2001665

Brookshire, G., Lu, J., Nusbaum, H. C., Goldin-Meadow, S., & Casasanto, D. (2017). Visual cortex entrains to sign language. Proceedings of the National Academy of Sciences, 114(24), 6352–6357. https://doi.org/10.1073/pnas.1620350114

Doelling, K. B., & Poeppel, D. (2015). Cortical entrainment to music and its modulation by expertise. Proceedings of the National Academy of Sciences, 112(45), E6233–E6242. https://doi.org/10.1073/pnas.1508431112

Henry, M. J., Herrmann, B., & Obleser, J. (2014). Entrained neural oscillations in multiple frequency bands comodulate behavior. Proceedings of the National Academy of Sciences, 111(41), 14935–14940. https://doi.org/10.1073/pnas.1408741111

Keitel, C., Keitel, A., Benwell, C. S. Y., Daube, C., Thut, G., & Gross, J. (2019). Stimulus-Driven Brain Rhythms within the Alpha Band: The Attentional-Modulation Conundrum. The Journal of Neuroscience, 39(16), 3119–3129. https://doi.org/10.1523/JNEUROSCI.1633-18.2019

Lakatos, P., Gross, J., & Thut, G. (2019). A New Unifying Account of the Roles of Neuronal Entrainment. Current Biology, 29(18), R890–R905. https://doi.org/10.1016/j.cub.2019.07.075

Morillon, B., Schroeder, C. E., Wyart, V., & Arnal, L. H. (2016). Temporal Prediction in lieu of Periodic Stimulation. Journal of Neuroscience, 36(8), 2342–2347. https://doi.org/10.1523/JNEUROSCI.0836-15.2016

Notbohm, A., Kurths, J., & Herrmann, C. S. (2016). Modification of Brain Oscillations via Rhythmic Light Stimulation Provides Evidence for Entrainment but Not for Superposition of Event-Related Responses. Frontiers in Human Neuroscience, 10. https://doi.org/10.3389/fnhum.2016.00010

Obleser, J., & Kayser, C. (2019). Neural Entrainment and Attentional Selection in the Listening Brain. Trends in Cognitive Sciences, 23(11), 913–926. https://doi.org/10.1016/j.tics.2019.08.004

Zoefel, B., ten Oever, S., & Sack, A. T. (2018). The Involvement of Endogenous Neural Oscillations in the Processing of Rhythmic Input: More Than a Regular Repetition of Evoked Neural Responses. Frontiers in Neuroscience, 12. https://doi.org/10.3389/fnins.2018.00095

Reviewer #3 (Public Review):

The current experiment tests whether the attentional blink is affected by higher-order regularity based on rhythmic organization of contextual features (pitch, color, or motion). The results show that this is indeed the case: the AB effect is smaller when two targets appeared in two adjacent cycles (between-cycle condition) than within the same cycle defined by the background sounds. Experiment 2 shows that this also holds for temporal regularities in the visual domain and Experiment 3 for motion. Additional EEG analysis indicated that the findings obtained can be explained by cortical entrainment to the higher-order contextual structure. Critically feature-based structure of contextual rhythms at 2.5 Hz was correlated with the strength of the attentional modulation effect.

This is an intriguing and exciting finding. It is a clever and innovative approach to reduce the attention blink by presenting a rhythmic higher-order regularity. It is convincing that this pulling out of the AB is driven by cortical entrainment. Overall, the paper is clear, well written and provides adequate control conditions. There is a lot to like about this paper. Yet, there are particular concerns that need to be addressed. Below I outline these concerns:

1) The most pressing concern is the behavioral data. We have to ensure that we are dealing here with a attentional blink. The way the data is presented is not the typical way this is done. Typically in AB designs one see the T2 performance when T1 is ignored relative to when T1 has to be detected. This data is not provided. I am not sure whether this data is collected but if so the reader should see this.

Many thanks for the suggestion. We appreciate the reviewer for his/her thoughtful comments. To demonstrate the AB effect, we did include two T2 lag conditions in our study (Experiments 1a, 1b, 2a, and 2b)—a short-SOA condition where T2 was located at the second lag of T1 (i.e., SOA = 200 ms), and a long-SOA condition where T2 appeared at the 8th lag of T1 (i.e., SOA = 800 ms). In a typical AB effect, T2 performance at short lags is remarkably impaired compared with that at long lags. In our study, we consistently replicated this effect across the experiments, as reported in the Results section of Experiment 1 (page 5, line 106). Overall, the T2 detection accuracy conditioned on correct T1 response was significantly impaired in the short-SOA condition relative to that in the long-SOA condition (mean accuracy > 0.9 for all experiments), during both the context session and the baseline session. More crucially, when looking into the magnitude of the AB effect as measured by (ACClong-SOA - ACCshort-SOA)/ACClong-SOA, we still obtained a significant attentional modulation effect (for Experiment 1a, t(15) = -2.729, p = .016, Cohen’s d = 0.682; for Experiment 2a, t(15) = -4.143, p <.001, Cohen’s d = 1.036) similar to that reflected by the short-SOA condition alone, further confirming that cortical entrainment effectively influences the AB effect.

Although we included both the long- and short-SOA conditions in the current study, we focused on T2 performance in the short-SOA condition rather than along the whole AB curve for the following reasons. Firstly, for the long-SOA conditions, the T2 performance is at ceiling level, making it an inappropriate baseline to probe the attentional modulation effect. We focused on Lag 2 because previous research has identified a robust AB effect around the second lag (Raymond et al., 1992), which provides a reasonable and sensitive baseline to probe the potential modulation effect of the contextual auditory and visual rhythms. Note that instead of using multiple lags, we varied the length of the rhythmic cycles (i.e., a cycle of 300 ms, 400 ms, and 500 ms corresponding to a rhythm frequency of 3.3 Hz, 2.5 Hz, and 2 Hz, respectively, all within the delta band), and showed that the attentional modulation effect could be generalized to these different delta-band rhythmic contexts, regardless of the absolute positions of the targets within the rhythmic cycles.

As to the T1 performance, the overall accuracy was very high, ranging from 0.907 to 0.972, in all of our experiments. The corresponding results have been added to the Results section of the revised manuscript (page 5, line 103). Notably, we did not find T1-T2 trade-offs in most of our experiments, except in Experiment 2a where T1 performance showed a moderate decrease in the between-cycle condition relative to that in the within-cycle condition (mean ± SE: 0.888 ± 0.026 vs. 0.933 ± 0.016, respectively; t(15) = -2.217, p = .043). However, by examining the relationship between the modulation effects (i.e., the difference between the two experimental conditions) on T1 and T2, we did not find any significant correlation (p = .403), suggesting that the better performance for T2 was not simply due to the worse performance in detecting T1.

Finally, previous studies have shown that ignoring T1 would lead to ceiling-level T2 performance (Raymond et al., 1992). Therefore, we did not include such manipulation in the current study, as in that case, it would be almost impossible for us to detect any contextual modulation effect.

References:

Raymond, J. E., Shapiro, K. L., & Arnell, K. M. (1992). Temporary suppression of visual processing in an RSVP task: An attentional blink? Journal of Experimental Psychology: Human Perception and Performance, 18(3), 849–860. https://doi.org/10.1037/0096-1523.18.3.849

2) Also, there is only one lag tested. The ensure that we are dealing here with a true AB I would like to see that more than one lag is tested. In the ideal situation a full AB curve should be presented that includes several lags. This should be done for at least for one of the experiments. It would be informative as we can see how cortical entrainment affects the whole AB curve.

Many thanks for the suggestion. Please refer to our response to the point #1 for “Reviewer #3 (Public Review)”. In short, we did include two T2 lag conditions in our study (Experiments 1a, 1b, 2a and 2b), and the results replicated the typical AB effect. We have clarified this point in the revised manuscript (page 5, line 106).

3) Also, there is no data regarding T1 performance. It is important to show that this the better performance for T2 is not due to worse performance in detecting T1. So also please provide this data.

Many thanks for the suggestion. Please refer to our response to the point #1 or “Reviewer #3 (Public Review)”. We have reported the T1 performance in the revised manuscript (page 5, line 103), and the results didn’t show obvious T1-T2 trade-offs.

4) The authors identify the oscillatory characteristics of EEG signals in response to stimulus rhythms, by examined the FFT spectral peaks by subtracting the mean power of two nearest neighboring frequencies from the power at the stimulus frequency. I am not familiar with this procedure and would like to see some justification for using this technique.

According to previous studies (Nozaradan, 2011; Lenc e al., 2018), the procedure to subtract the average amplitude of neighboring frequency bins can remove unrelated background noise, like muscle activity or eye movement. If there were no EEG oscillatory responses characteristic of stimulus rhythms, the amplitude at a given frequency bin should be similar to the average of its neighbors, and thus no significant peaks could be observed in the subtracted spectrum.

References:

Lenc, T., Keller, P. E., Varlet, M., & Nozaradan, S. (2018). Neural tracking of the musical beat is enhanced by low-frequency sounds. Proceedings of the National Academy of Sciences, 115(32), 8221–8226. https://doi.org/10.1073/pnas.1801421115

Nozaradan, S., Peretz, I., Missal, M., & Mouraux, A. (2011). Tagging the Neuronal Entrainment to Beat and Meter. The Journal of Neuroscience, 31(28), 10234–10240. https://doi.org/10.1523/JNEUROSCI.0411-11.2011

Author Response

Summary:

This work is of interest because it increases our understanding of the molecular mechanisms that distinguish subtypes of VIP interneurons in the cerebral cortex and because of the multiple ways in which the authors address the role of Prox1 in regulating synaptic function in these cells.

The authors would like to thank the reviewers for their constructive comments. In response, we would like to clarify a number of issues, as well as outline how we plan to resolve major concerns.

Reviewer #1:

Stachiak and colleagues examine the physiological effects of removing the homeobox TF Prox1 from two subtypes of VIP neurons, defined on the basis of their bipolar vs. multipolar morphology.

The results will be of interest to those in the field, since it is known from prior work that VIP interneurons are not a uniform class and that Prox1 is important for their development.

The authors first show that selective removal of a conditional Prox1 allele using a VIP cre driver line results in a change in paired pulse ratio of presumptive excitatory synaptic responses in multipolar but not bipolar VIP interneurons. The authors then use RNA-seq to identify differentially expressed genes that might contribute and highlight a roughly two-fold reduction in the expression of a transcript encoding a trans-synaptic protein Elfn1 known to contribute to reduced glutamate release in Sst+ interneurons. They then test the potential contribution of Elfn1 to the phenotype by examining whether loss of one allele of Elfn1 globally alters facilitation. They find that facilitation is reduced both by this genetic manipulation and by a pharmacological blockade of presynaptic mGluRs known to interact with Elfn1.

Although the results are interesting, and the authors have worked hard to make their case, the results are not definitive for several reasons:

1) The global reduction of Elfn1 may act cell autonomously, or may have other actions in other cell types. The pharmacological manipulation is less subject to this interpretation, but these results are not as convincing as they could be because the multipolar Prox1 KO cells (Fig. 3 J) still show substantial facilitation comparable, for example to the multipolar control cells in the Elfn1 Het experiment (controls in Fig. 3E). This raises a concern about control for multiple comparisons. Instead of comparing the 6 conditions in Fig 3 with individual t-tests, it may be more appropriate to use ANOVA with posthoc tests controlled for multiple comparisons.

The reviewer’s concerns regarding non-cell-autonomous actions of global Elfn1 KO are well founded. Significant phenotypic alterations have previously been reported, both in the physiology of SST neurons as well in the animals’ behavior (Stachniak, Sylwestrak, Scheiffele, Hall, & Ghosh, 2019; Tomioka et al., 2014). The homozygous Elfn1 KO mouse displays a hyperactive phenotype and epileptic activity after 3 months of age, suggesting generalcortical activity differences exist (Dolan & Mitchell, 2013; Tomioka et al., 2014). Nevertheless, we have not observed such changes in P17-21 Elfn1 heterozygous (Het) animals.

Comparing across different experimental animal lines, for example the multipolar Prox1 KO cells (Fig. 3 J) to the multipolar control cells in the Elfn1 Het experiment (controls in Fig. 3E), is in our view not advisable. There is a plethora of examples in the literature on the effect of mouse strain on even the most basic cellular functions and hence it is always expected that researchers use the correct control animals for their experiments, which in the best case scenario are littermate controls. For these reasons, we would argue that statistical comparisons across mouse lines is not ideal for our study. Elfn1 Het and MSOP data are presented side by side to illustrate that Elfn1 Hets (3C,E) phenocopy the effects of Prox1 deletion (3G,H,I,J). (See also point 3) MSOP effect sizes, however, do show significant differences by ANOVA with Bonferroni post-hoc (normalized change in EPSC amplitude; multipolar prox1 control: +12.1 ± 3.8%, KO: -8.4 ± 4.3%, bipolar prox1 control: -5.2 ± 4.3%, KO: -3.4 ± 4.7%, cell type x genotype interaction, p= 0.02, two way ANOVA).

2) The isolation of glutamatergic currents is not described. Were GABA antagonists present to block GABAergic currents? Especially with the Cs-based internal solutions used, chloride reversal potentials can be somewhat depolarized relative to the -65 mV holding potential. If IPSCs were included it would complicate the analysis.

No, in fact GABA antagonists were not present in these experiments. The holding voltage in our evoked synaptic experiments is -70 mV, which combined with low internal [Cl-] makes it highly unlikely that the excitatory synaptic responses we study are contaminated by GABA-mediated ones, even with a Cs MeSO4-based solution. Nevertheless, we have now performed additional experiments where glutamate receptor blockers were applied in bath and we observe a complete blockade of the synaptic events at -70mV proving that they are AMPA/NMDA receptor mediated. When holding the cell at 0mV with these blockers present, outward currents were clearly visible, suggesting intact GABA-mediated events.

3) The assumption that protein levels of Elfn1 are reduced to half in the het is untested. Synaptic proteins can be controlled at the level of translation and trafficking and WT may not have twice the level of this protein.

We thank reviewer for pointing this out. Our rationale for using the Elfn1 heterozygous animals is rather that transcript levels are reduced by half in heterozygous animals, to match the reduction we found in the mRNA levels of VIP Prox1 KO cells (Fig 2). The principle purpose of the Elfn1 KO experiment was to determine whether the change in Elfn1 transcript levels could be sufficient to explain the synaptic deficit observed in VIP Prox1 KO cells. As the reviewer notes, translational regulation and protein trafficking could ultimately result in even larger changes than 0.5x protein levels at the synapse. This may ultimately explain the observed multipolar/bipolar disparity, which cannot be explained by transcriptional regulation alone (Fig 4).

4) The authors are to be commended for checking whether Elfn1 is regulated by Prox1 only in the multipolar neurons, but unfortunately it is not. The authors speculate that the selective effects reflect a selective distribution of MgluR7, but without additional evidence it is hard to know how likely this explanation is.

Additional experiments are underway to better understand this mechanism.

Reviewer #2:

Stachniak et al., provide an interesting manuscript on the postnatal role of the critical transcription factor, Prox1, which has been shown to be important for many developmental aspects of CGE-derived interneurons. Using a combination of genetic mouse lines, electrophysiology, FACS + RNAseq and molecular imaging, the authors provide evidence that Prox1 is genetically upstream of Elfn1. Moreover, they go on to show that loss of Prox1 in VIP+ cells preferentially impacts those that are multipolar but not the bipolar subgroup characterized by the expression of calretinin. This latter finding is very interesting, as the field is still uncovering how these distinct subgroups emerge but are at a loss of good molecular tools to fully uncover these questions. Overall, this is a great combination of data that uses several different approaches to come to the conclusions presented. I have suggestions that I think would strengthen the manuscript:

1) Can the authors add a supplemental table showing the top 20-30 genes up and down regulated in their Prox1 KOS? This would make these, and additional, data more tenable to readers.

We would be happy to provide supplementary tables with candidate genes at both P8 and P12.

2) It is interesting that loss of Prox1 or Elfn1 leads to phenotypes in multipolar but are not present or mild in bipolar VIP+ cells. The authors test different hypotheses, which they are able to refute and discuss some ideas for how multipolar cells may be more affected by loss of Elfn1, even when the transcript is lost in both multipolar and bipolar after Prox1 deletion. If there is any way to expand upon these ideas experimentally, I believe it would greatly strengthen the manuscript. I understand there is no perfect experiment due to a lack of tools and reagents but if there is a way to develop one of the following ideas or something similar, it would be beneficial:

We thank the reviewer for the note.

a) Would it be possible to co-fill VIPCre labeled cells with biocytin and a retroviral tracer? Then, after the retroviral tracer had time to label a presynaptic cell, assess whether these were preferentially different between bipolar and multipolar cell types, the latter morphology determined by the biocytin fill? This would test whether each VIP+ subtype is differentially targeted.

Although this is a very elegant experiment and we would be excited to do it, we do feel that single-cell rabies virus tracing is technically very challenging and will take many months to troubleshoot before being able to acquire good data. Hence, we think it is beyond the scope of this study.

b) Another biocytin possibility would be to trace filled VIP+ cells and assess whether the dendrites of multipolar and bipolar cells differentially targeted distinct cortical lamina and whether these lamina, in the same section or parallel, were enriched for mGluR7+ afferents.

We thank the reviewer for their suggestion and we are planning on doing these kinds of experiments.

Reviewer #3:

In this work Stachiak and colleagues investigate the role of Prox1 on the development of VIP cells. Prox1 is expressed by the majority of GABAergic derived from the caudal ganglionic eminence (CGE), and as mentioned by the authors, Prox1 has been shown to be necessary for the differentiation, circuit integration, and maintenance of CGE-derived GABAergic cells. Here, Stachiak and colleagues show that removal of Prox1 in VIP cells leads to suppression of synaptic release probability onto cortical multipolar VIP cells in a mechanism dependent on Elfn1. This work is of interest for the field because it increases our understanding of differential synaptic maturation of VIP cells. The results are noteworthy, however the relevance of this manuscript would potentially be increased by addressing the following suggestions:

1) Include histology to show when exactly Prox1 is removed from multipolar and bipolar VIP-expressing cells by using the VIP-Cre mouse driver.

We can address this by performing an in-situ hybridization against Prox1 from P3 onwards (when Cre becomes active).

2) Clarify if the statistical analysis is done using n (number of cells) or N (number of animals). The analysis between control and mutants (both Prox1 and Elfn1) need to be done across animals and not cells.

Statistics for physiology were done across n (number of cells) while statistics for ISH are done across number of slices. We will clarify this point in the text and update the methods.

Regarding the statistics for the ISH, these have been done across n (number of slices) for control versus KO tissue (N = 3 and N = 2 animals, respectively). We will add more animals to this analysis to compare by animal instead, although we do not expect any change in the results.

Regarding the physiology, we would provide a two-pronged answer. We first of all feel that averaging synaptic responses for each animal would hide a good deal of the biological variability in PPR present in different cells (response Fig 1), the characterization of which is integral to the central findings of the paper. Secondly, to perform such analysis asked by the reviewer one would need to obtain recordings from ~10 animals or so per condition for each condition, which, to our knowledge, is something that is not standard when utilizing in vitro electrophysiological recordings from single cells. For example, in these very recent studies that have performed in vitro electrophysiological recordings all the statistics are performed using “n” number of cells and not the average of all the cells recorded per animal collapsed into a single data point. (Udakis, Pedrosa, Chamberlain, Clopath, & Mellor, 2020) https://www.nature.com/articles/s41467-020-18074-8

(Horvath, Piazza, Monteggia, & Kavalali, 2020) https://elifesciences.org/articles/52852

(Haas et al., 2018) https://elifesciences.org/articles/31755

Nevertheless, we have now re-run the analysis grouping the cells and averaging the values we get per animal, since we have obtained our data from many animals. The results are more or less indistinguishable from the ones presented in the original submission, except for on p value that rose to 0.07 from 0.03 due to the lack of the required number of animals. We hope that the new plots and statistics presented herein address the concern put forward by the reviewer.

Response Fig 1: A comparison of cell wise versus animal-wise analysis of synaptic physiology. Some cell to cell variability is hidden, and the reduction in numbers impacts the P values.

(A) PPR of multipolar Prox1 Control for 14 cells from 9 animals (n/N=14/9) under baseline conditions and with MSOP, cell-wise comparison p = 0.02 , t = 2.74 and (B) animal-wise comparisons (p = 0.04, t stat = 2.45). Statistics: paired t-test.

(C) PPR of multipolar Prox1 KO cells (n/N=9/8) under baseline conditions and with MSOP, cell-wise comparison p = 0.2, t = 1.33 and (D) animal-wise comparisons (p = 0.2, t stat = 1.56). Statistics: paired t-test. Comparisons for PPR of bipolar Prox1 Control (n/N=8/8) and KO cells (n/N=9/9) did not change.

(E) PPR for Prox1 control (n/N=18/11) and KO (n/N=13/11) bipolar VIP cells, cell-wise comparison p = 0.3, t = 1.1 and (F) animal-wise comparisons (p = 0.4, t stat = 0.93). Statistics: t-test.

(G) PPR of Elfn1 Control (n/N=12/4) and Het (n/N=12/4) bipolar VIP cells, cell-wise comparison p = 0.3, t = 1.06 and (H) animal-wise comparisons (p = 0.4, t stat = 0.93)

(I) PPR of Prox1 control (n/N=33/18) and KO (n/N=19/14) multipolar VIP cells, cell-wise comparison p = 0.03, t = 2.17. and (J) animal-wise comparisons (p = 0.07, t stat = 1.99).

(K) PPR of Elfn1 Control (n/N=14/6) and Het (n/N=20/8) multipolar VIP cells, cell-wise comparison p = 0.008, t = 2.84 and (L) animal-wise comparisons (p = 0.007, t stat = 3.23).

3) Clarify what are the parameters used to identify bipolar vs multipolar VIP cells. VIP cells comprise a wide variety of transcriptomic subtypes, and in the absence of using specific genetic markers for the different VIP subtypes, the authors should either include the reconstructions of all recorded cells or clarify if other methods were used.

We thank the reviewer for this comment. The cell parameter criteria will be amended in the methods: “Cell type was classified as bipolar vs. multipolar based on cell body morphology (ovoid vs. round) and number and orientation of dendritic processes emanating from it (2 or 3 dendrites perpendicular to pia (for bipolar) vs. 3 or more processes in diverse orientations (for multipolar). In addition, the laminar localization of the two populations differs, with multipolar cells found primarily in the upper layer 2, while bipolar cells are found throughout layers 2 and 3. Initial determination of cell classification was made prior to patching fluorescent-labelled cells, but whenever possible this initial assessment was confirmed with post-hoc verification of biocytin filled cells.”

Reference:

Dolan, J., & Mitchell, K. J. (2013). Mutation of Elfn1 in Mice Causes Seizures and Hyperactivity. PLOS ONE, 8(11), e80491. Retrieved from https://doi.org/10.1371/journal.pone.0080491

Haas, K. T., Compans, B., Letellier, M., Bartol, T. M., Grillo-Bosch, D., Sejnowski, T. J., … Hosy, E. (2018). Pre-post synaptic alignment through neuroligin-1 tunes synaptic transmission efficiency. ELife, 7, e31755. https://doi.org/10.7554/eLife.31755

Horvath, P. M., Piazza, M. K., Monteggia, L. M., & Kavalali, E. T. (2020). Spontaneous and evoked neurotransmission are partially segregated at inhibitory synapses. ELife, 9, e52852. https://doi.org/10.7554/eLife.52852

Stachniak, T. J., Sylwestrak, E. L., Scheiffele, P., Hall, B. J., & Ghosh, A. (2019). Elfn1-Induced Constitutive Activation of mGluR7 Determines Frequency-Dependent Recruitment of Somatostatin Interneurons. The Journal of Neuroscience, 39(23), 4461 LP – 4474. https://doi.org/10.1523/JNEUROSCI.2276-18.2019

Tomioka, N. H., Yasuda, H., Miyamoto, H., Hatayama, M., Morimura, N., Matsumoto, Y., … Aruga, J. (2014). Elfn1 recruits presynaptic mGluR7 in trans and its loss results in seizures. Nature Communications. https://doi.org/10.1038/ncomms5501

Udakis, M., Pedrosa, V., Chamberlain, S. E. L., Clopath, C., & Mellor, J. R. (2020). Interneuron-specific plasticity at parvalbumin and somatostatin inhibitory synapses onto CA1 pyramidal neurons shapes hippocampal output. Nature Communications, 11(1), 4395. https://doi.org/10.1038/s41467-020-18074-8

Author Response

Reviewer #1:

The Lambowitz group has developed thermostable group II intron reverse transcriptases (TGIRTs) that strand switch and also have trans-lesion activity to provide a much wider view of RNA species analyzed by massively parallel RNA sequencing. In this manuscript they use several improvements to their methodology to identify RNA biotypes in human plasma pooled from several healthy individuals. Additionally, they implicate binding by proteins (RBPs) and nuclease-resistant structures to explain a fraction of the RNAs observed in plasma. Generally I find the study fascinating and argue that the collection of plasma RNAs described is an important tool for those interested in extracellular RNAs. I think the possibility that RNPs are protecting RNA fragments in circulation is exciting and fits with elegant studies of insects and plants where RNAs are protected by this mechanism and are transmitted between species.

I have one major comment for the authors to consider. In my view the use of pooled plasma samples prevented the important opportunity to provide a glimpse on human variation in plasma RNA biotypes. This significantly limits the use of this information to begin addressing RNA biotypes as biomarkers. While I realize that data from multiple individuals represents a significant undertaking and may be beyond the scope of this manuscript, I urge the authors to do two things: (1) downplay the significance of the current study on the development of biomarkers in the current manuscript (e.g., in the abstract and discussion - e.g., "The ability of TGIRT-seq to simultaneously profile a wide variety of RNA biotypes in human plasma, including structured RNAs that are intractable to retroviral RTs, may be advantageous for identifying optimal combinations of coding and non-coding RNA biomarkers for human diseases."). (2) Carry out an analysis in multiple individuals - including racially diverse individuals - very important information will come of this - similar to C. Burge's important study in Nature ~2008 where it was clear that there is important individual variation in alternative splicing decisions - very likely genetically determined. This second suggestion could be added here or constitute a future manuscript.

The identification of biomarkers in human plasma is an important application of this study, as was noted by reviewer 3 -- "Overall, this study provided a robust dataset and expanded picture of RNA biotypes one can detect in human plasma. This is valuable because the findings may have implications in biomarker identification in disease contexts." The present manuscript lays the foundation for such applications, which we have been carrying out in parallel. In one such study in collaboration with Dr. Naoto Ueno (MD Anderson), we used TGIRT-seq to identify combinations of mRNA and non-coding RNA biomarkers in FFPE-tumor slices, PBMCs and plasma from inflammatory breast cancer patients compared to non-IBC breast cancer patients and healthy controls (manuscript in preparation; data presented publicly in seminars), and in another, we explored the potential of using full-length excised intron (FLEXI) RNAs as biomarkers. In the latter study, we identified >8,000 FLEXI RNAs in different human cell lines and tissues and found that they are expressed in a cell-type specific manner, including hundreds of differences between matched tumor and healthy tissues from breast cancer patients and cell lines. A manuscript describing the latter findings was submitted for publication after this one and has been uploaded as a pertinent related manuscript. This new manuscript follows directly from the last sentence of the present manuscript and fully references the BioRxiv preprint currently under review for eLife.

Reviewer #2:

Yao et al used thermostable group II intron reverse transcriptase sequencing (TGIRT-seq) to study apheresis plasma samples. The first interesting discovery is that they had identified a number of mRNA reads with putative binding sites of RNA-binding proteins. A second interesting discovery from this work is the detection of full-length excised intron RNAs.

I have the following comments:

1) One doubt that I have is how representative is apheresis plasma when compared with plasma that one obtains through routine centrifugation of blood. The authors have reported the comparison of apheresis plasma versus a single male plasma in a previous publication. I think that to address this important question, a much increased number of samples would be necessary.

Detailed comparison of plasma prepared by apheresis to that prepared by centrifugation would require a separate large-scale study, preferably by multiple laboratories using different methods to prepare plasma. However, our impression both from our findings and from the literature (Valbonesi et al. 2001, cited in the manuscript) is that apheresis-prepared plasma has very low levels of cellular contamination (required to meet clinical standards) compared to plasma prepared by centrifugation, even with protocols designed to minimize contamination from intact 4 or broken cell (e.g., preparing plasma from freshly drawn blood, centrifugation into a Ficoll cushion to minimize cell breakage, and carefully avoiding contamination from sedimented cells).

We do have additional information about the degree of variation in protein-coding gene transcripts detected by TGIRT-seq in plasma samples prepared by centrifugation from five healthy females controls in our collaborative study with Dr. Naoto Ueno (M.D. Anderson; see above), and we have added it to the manuscript citing a manuscript in preparation with permission from Dr. Ueno (p. 10, beginning line 6 from bottom) as follows:

“The identities and relative abundances of different protein-coding gene transcripts in the apheresis-prepared plasma were broadly similar to those in the previous TGIRT analysis of plasma prepared by Ficoll-cushion sedimentation of blood from a healthy male individual (Qin et al., 2016) (r = 0.62-0.80; Figure 3C) and between high quality plasma samples similarly prepared from five healthy females in a collaborative study with Dr. Naoto Ueno, M.D. Anderson (r = 0.53-0.67; manuscript in preparation).” See Author Response Image below.

2) For the important conclusion of the presence of binding sites of RNA-binding proteins in a proportion of apheresis plasma mRNA molecules, the authors need to explore whether there is any systemic difference in terms of mapping quality (i.e. mapping quality scores in alignment results) between RBP binding sites and non-RBP binding sites, so that any artifacts of peaks caused by the alignment issues occurring in RNA-seq analysis could be revealed and solved subsequently. Furthermore, it would be prudent to perform immunoprecipitation experiments to confirm this conclusion in at least a proportion of the mRNA.

We have added a figure panel comparing MAPQ scores for reads from peaks containing RBP-binding site to other long RNA reads (Figure 4–figure supplement 2A) and have added further details about the methods used to obtain peaks with high quality reads, including the following (p. 13, beginning line 3 from the bottom).

“After further filtering to remove read alignments with MAPQ <30 (a cutoff that eliminates reads mapping equally well at more than one locus) or ≥5 mismatches from the mapped locus, we were left with 950 high confidence peaks ranging in size from 59 to 1,207 nt with ≥5 high quality read alignments at the peak maximum (Supplementary File).”

3) In Fig. 2D, one can observe that there are clearly more RNA reads in TGIRT-seq located in the 1st exon of ACTB, compared with SMART-seq. Is there any explanation? Will this signal be called as a peak (a potential RBP binding site) in the peak calling analysis (MACS2)? Is ACTB supposed to be bound by a certain RBP?

The higher coverage of the ACTB 5'-exon in the TGIRT-seq datasets reflects in part the more uniform 5' to 3' coverage of mRNA sequences by TGIRT-seq compared to SMART-seq, which is biased for 3'-mRNA sequences that have poly(A) tails (current Figure 3F). The signal in the first exon of ACTB was in fact called as a peak by MACS2 (peak ID#893, Supplementary file), which overlapped an annotated binding site for SERBP1 (see Supplementary File).

4) For Fig 2A, it would be informative for the comparison of RNA yield and RNA size profile among different protocols if the author also added the results of TGIRT-seq.

Figure 3D (previously Figure 2A) shows a bioanalyzer trace of PCR amplified cDNAs obtained by SMART-Seq. These cDNAs correspond to 3' mRNA sequences that have poly(A) tails and are not comparable to the bioanalyzer profiles of plasma RNA (Figure 1–figure supplement 1) or read span distributions in the TGIRT-seq datasets (Figure 1B), which are dominated by sncRNAs. The coverage plots for protein-coding gene transcripts show that TGIRT-seq captures mRNA fragments irrespective of length that span the entire mRNA sequence, whereas SMART-seq is biased for 3' sequences linked to poly(A) (Figure 3F). We also note that coverage plots and mRNAs detected by TGIRT-seq remain similar, even if the plasma RNA is chemically fragmented prior to TGIRT-seq library construction (Figure 3F and Figure 3–figure supplement 2).

5) As shown in Figure 4 C (the track of RBP binding sites), it seems quite pervasive in some gene regions. How many RBP binding sites from public eCLIP-seq results are used for overlapping peaks present in TGIRT-seq of plasma RNA? What percentage of plasma RNA reads have fallen within RBP binding sites? Are those peaks present in TGRIT-seq significantly enriched in RBPs binding regions?

Some of these points are addressed under Reviewer 1-comment #4. Additionally, we noted that 109 RBP-binding sites were searched in the original analysis, and we have now added further analyses for 150 RBPs currently available in ENCODE eCLIP datasets with and without irreproducible discovery rate (IDR) analysis (Figure 6 and Figure 6–figure supplement 1). We have also added a tab to the Supplementary File identifying the 109 and 150 RBPs whose binding sites were searched. The requested statistical analysis has been added in Figure 4–figure supplement 2C. The analysis shows that enrichment of RBP-binding site sequences in the 467 called peaks was statistically significant (p<0.001) (p. 14, para. 3, last sentence).

6) Since there is a considerable portion of TGIRT-seq reads related to simple repeat, one possible reason is likely the high abundance of endogenous repeat-related RNA species in plasma. Nonetheless, have authors studied whether the ligation steps in TGIRT-seq have any biases (e.g. GC content) when analyzing human reference RNAs and spike ins (page 4, paragraph 2)?

We have added a note to the manuscript indicating that although repeat RNAs constitute a high proportion of the called peaks, they do not constitute a similarly high proportion of the total RNA reads (Figure 1C; p. 18, para. 2, first sentence). The TGIRT-seq analysis of human reference RNAs and spike-ins showed that TGIRT-seq recapitulates the relative abundance of human transcripts and spike-in comparably to non-strand-specific TruSeq v2 and better than strand-specific TruSeq v3 (Nottingham et al. RNA 2016). Subsequently, we used miRNA reference sets for detailed analysis of TGIRT-seq biases, including developing a computer algorithm for bias correction based on a random forest regression model that provides insight into different factors that contribute to these biases (Xu et al. Sci. Report. 2019). Overall GC content does not make a significant contribution to TGIRT-seq biases (Figure 9 of Xu et al. Sci. Report, 2017). Instead, biases in TGIRT-seq are largely confined to the first three nucleotides at the 5'-end (due to bias of the thermostable 5' App DNA ligase used for 5' RNA-seq adapter addition) and the 3' nucleotide (due to TGIRT-template switching). These end biases are not expected to significantly impact the quantitation of repeat RNAs.

7) As described in Figure 2 legend, there are 0.25 million deduplicated reads for TGIRT-seq reads assigned to protein-coding genes transcripts which are far less than 2.18 million reads for SMART-seq. The authors need to discuss whether the current protocol of TGIRT-seq would cause potential dropouts in mRNA analysis, compared with SMART-seq?

We have added the following to the manuscript (p. 11, para. 1, line 15).

“The larger number of mRNA reads compared to TGIRT-seq (0.28 million) largely reflects that SMART-seq selectively profiles polyadenylated mRNAs, while TGIRT-seq profiles mRNAs together with other more abundant RNA biotypes. In addition, ultra low input SMART-Seq is not strand-specific, resulting in redundant sense and antisense strand reads (Figure 3–figure supplement 1).”

The manuscript contains the following statement regarding potential drop outs (p. 11, para. 2, line 1).

“A scatter plot comparing the relative abundance of transcripts originating from different genes showed that most of the polyadenylated mRNAs detected in DNase I-treated plasma RNA by ultra low input SMART-Seq were also detected by TGIRT-seq at similar TPM values when normalized for protein-coding gene reads (r=0.61), but with some, mostly lower abundance mRNAs undetected either by TGIRT-seq or SMART-Seq, and with SMART-seq unable to detect non-polyadenylated histone mRNAs, which are relatively abundant in plasma (Figure 3E and Figure 3–figure supplement 1).”

8) While scientific thought-provoking, the practical implication of the current work is still unclear. The authors have suggested that their work might have applications for biomarker development. Is it possible to provide one experimental example in the manuscript?

We addressed the relevance of the manuscript to biomarker identification and noted parallel studies that supports this application in the response to reviewer 1--comment 1. We have also modified the final paragraph of the Discussion (p. 30, para. 2).

“The ability of TGIRT-seq to simultaneously profile a wide variety of RNA biotypes in human plasma, including structured RNAs that are intractable to retroviral RTs, may be advantageous for identifying optimal combinations of coding and non-coding RNA biomarkers that could then be incorporated in target RNA panels for diagnosis and routine monitoring of disease progression and response to treatment. The finding that some mRNAs fragments persist in discrete called peaks suggests a strategy for identifying relatively stable mRNA regions that may be more reliably detected than other more labile regions in targeted liquid biopsies. Finally, we note that in addition to their biological and evolutionary interest, short full-length excised intron RNAs and intron RNA fragments, such as those identified here, may be uniquely well suited to serve as stable RNA biomarkers, whose expression is linked to that of numerous protein-coding genes."

Reviewer #3:

In this work, Yao and colleagues described transcriptome profiling of human plasma from healthy individuals by TGIRT-seq. TGIRT is a thermostable group II intron reverse transcriptase that offers improved fidelity, processivity and strand-displacement activity, as compared to standard retroviral RT, so that it can read through highly structured regions. Similar analysis was performed previously (ref. 20), but this study incorporated several improvements in library preparation including optimization of template switching condition and modified adapters to reduce primer dimer and introduce UMI. In their analysis, the authors detected a variety of structural RNA biotypes, as well as reads from protein-coding mRNAs, although the latter is in low abundance. Compared to SMART-Seq, TGIRT-seq also achieved more uniform read coverage across gene bodies. One novel aspect of this study is the peak analysis of TGIRT-seq reads, which revealed ~900 peaks over background. The authors found that these peaks frequently overlap with RBP binding sites, while others tend to have stable predicted secondary structures, which explains why these regions are protected from degradation in plasma. Overall, this study provided a robust dataset and expanded picture of RNA biotypes one can detect in human plasma. This is valuable because the findings may have implications in biomarker identification in disease contexts. On the other hand, the manuscript, in the current form, is relatively descriptive, and can be improved with a clearer message of specific knowledge that can be extracted from the data.

Specific points:

1) Several aspects of bioinformatics analysis can be clarified in more detail. For example, it is unclear how sequencing errors in UMI affect their de-duplication procedure. This is important for their peak analysis, so it should be explained clearly.

We have added details of the procedure used for de-duplication to the following paragraph in Materials and methods (p. 35, para. 2).

“Deduplication of mapped reads was done by UMI, CIGAR string, and genome coordinates (Quinlan, 2014). To accommodate base-calling and PCR errors and non-templated nucleotides that may have been added to the 3' ends of cDNAs during TGIRT-seq library preparation, one mismatch in the UMI was allowed during deduplication, and fragments with the same CIGAR string, genomic coordinates (chromosome start and end positions), and UMI or UMIs that differed by one nucleotide were collapsed into a single fragment. The counts for each read were readjusted to overcome potential UMI saturation for highly-expressed genes by implementing the algorithm described in (Fu et al., 2011), using sequencing tools (https://github.com/wckdouglas/sequencing_tools ).”

Also, it is not described how exon junction reads (when mapped to the genome) are handled in peak calling, although the authors did perform complementary analysis by mapping reads to the reference transcriptome.

We have added this to first sentence of the paragraph describing peak calling against the transcriptome reference (p. 16, line 4), which now reads as follows:

"Peak calling against the human genome reference sequence might miss RBP-binding sites that are close to or overlap exon junctions, as such reads were treated by MACS2 as long reads that span the intervening intron."

2) Overall, the authors provided convincing data that TGIRT-seq has advantages in detecting a wide range of RNA biotypes, especially structured RNAs, compared to other protocols, but these data are more confirmatory, rather than completely new findings (e.g., compared to ref. 20).

As indicated in the response to Reviewer 1, comment 2, we modified the first paragraph of the Discussion to explicitly describe what is added by the present manuscript compared to Qin et al. RNA 2016 (p. 24, para. 2). Additionally, further analysis in response to the reviewers' comments resulted in the interesting finding that stress granule proteins comprised a high proportion of the RBPs whose binding sites were enriched in plasma RNAs (to our knowledge a completely new finding), consistent with a previously suggested link between RNP granules, EV packing, and RNA export (p. 16, last sentence; data shown in Figure 6 and Figure 6–figure supplement 1). Also highlighted in the Discussion p. 26, last sentence, continuing on p. 27).

3) The peak analysis is more novel. The authors observed that 50% of peaks in long RNAs overlap with eCLIP peaks. However, there is no statistical analysis to show whether this overlap is significant or simply due to the pervasive distribution of eCLIP peaks. In fact, it was reported by the original authors that eCLIP peaks cover 20% of the transcriptome.

We have added statistical analysis, which shows that the enrichment of RBP-binding sites in the 467 called peaks is statistically significant at p<0.001 (p. 14, para. 3, last sentence; Figure 4–Figure supplement 2C), as well as scatter plots identifying proteins whose binding sites were more highly represented in plasma than cellular RNAs or vice versa (p. 16, last two sentences; Figure 6 and Figure 6-figure supplement 1).

Similarly, the authors found that a high proportion of remaining peaks can fold into stable secondary structures, but this claim is not backed up by statistics either.

First, near the beginning of the paragraph describing these findings, we added the following to provide a guide as to what can and can't be concluded by RNAfold (p. 17, line 6 from the bottom).

"To evaluate whether these peaks contained RNAs that could potentially fold into stable secondary structures, we used RNAfold, a tool that is widely used for this purpose with the understanding that the predicted structures remain to be validated and could differ under physiological conditions or due to interactions with proteins."

Second, at the end of the same paragraph, we have added the requested statistics (p. 18, para. 1, last sentence).

"Subject to the caveats above regarding conclusions drawn from RNAfold, simulations using peaks randomly generated from long RNA gene sequences indicated that enrichment of RNAs with more stable secondary structures (lower MFEs) in the called RNA peaks was statistically significant (p≤0.019; Figure 4–figure supplement 2D)."

4) Ranking of RBPs depends on the total number of RBP binding sites detected by eCLIP, which is determined by CLIP library complexity and sequencing depth. This issue should be at least discussed.

We have added scatter plots in Figure 6 and Figure 6–figure supplement 1, which show that the relative abundance of different RBP-binding sites detected in plasma differs markedly from that for cellular RNAs in the eCLIP datasets (both for the 109 RBPs searched initially and for 150 RBPs with or without irreproducible discovery rate (IDR) analysis from the ENCODE web site,) As mentioned in comments above, this analysis identified a number of RBP-binding sites that were substantially enriched in plasma RNAs compared to cellular RNAs or vice versa and led to what we think is the important new finding that plasma RNAs are enriched binding sites for a number of stress granule proteins (Figure 6 and Figure 6–figures supplement 1). We thank the reviewers for this and related comments that led to this additional analysis.

5) Enrichment of RBP binding sites and structured RNA in TGIRT-seq data is certainly consistent with one's expectation. However, the paper can be greatly improved if the authors can make a clearer case of what is new that can be learned, as compared to eCLIP data or other related techniques that purify and sequence RNA fragments crosslinked to proteins. What is the additional, independent evidence to show the predicted secondary structures are real?

Compared to CLIP and related methods, peak calling enables more facile identification of candidate RBPs and putatively structured RNAs for further analysis and may be particularly useful for the vanishingly small amounts of RNA present in plasma and other bodily fluids. New findings resulting from peak calling in the present manuscript include that plasma RNAs are enriched in binding sites for stress granule proteins (see above) and the discovery of a variety of novel RNAs, including the full-length excised intron RNAs first identified here and subsequently studied in cellular RNAs in the Yao et al. pertinent submitted manuscript. We also note that peak calling enables the identification of protein-protected and structured mRNA regions that are relatively stable in plasma and may be more reliably detected in targeted liquid biopsy assays than are more labile mRNA regions (p. 17, para. 1, last sentence; and p. 30, para. 2, beginning on line 5).

6) The authors should probably discuss how alignment errors can potentially affect detection of repetitive regions.

In the Empirical Bayes method that we used for the analysis of repeats, repeat sequences were quantified by aggregate counts irrespective of the genomic locus to which they mapped (Materials and methods, p. 38, para. 2, line 5), which should not be affected by alignment errors.

7) Many figures are IGV screenshots, which can be difficult to follow. Some of them can probably be summarized to deliver the message better.

Some IGV-based figures are crucial for showing key features of the RNAs that are called as peaks (e.g., the predicted secondary structures of the full-length excised intron RNAs and intron RNA fragments). However, in the process of reformatting, we have switched in and added non-IGV main text figures including Figure 2 (microbiome analysis), Figure 3 (TGIRT-seq versus SMART-Seq), Figure 4 (repeats), and Figure 6 (new figure comparing relative abundance of RBP-binding sites in plasma versus cells).

Author Response:

Reviewer #1 (Public Review):

Strengths:

1) The model structure is appropriate for the scientific question.

2) The paper addresses a critical feature of SARS-CoV-2 epidemiology which is its much higher prevalence in Hispanic or Latino and Black populations. In this sense, the paper has the potential to serve as a tool to enhance social justice.

3) Generally speaking, the analysis supports the conclusions.

Other considerations:

1) The clean distinction between susceptibility and exposure models described in the paper is conceptually useful but is unlikely to capture reality. Rather, susceptibility to infection is likely to vary more by age whereas exposure is more likely to vary by ethnic group / race. While age cohort are not explicitly distinguished in the model, the authors would do well to at least vary susceptibility across ethnic groups according to different age cohort structure within these groups. This would allow a more precise estimate of the true effect of variability in exposures. Alternatively, this could be mentioned as a limitation of the the current model.

We agree that this would be an important extension for future work and have indicated this in the Discussion, along with the types of data necessary to fit such models:

“Fourth, due to data availability, we have only considered variability in exposure due to one demographic characteristic; models should ideally strive to also account for the effects of age on susceptibility and exposure within strata of race and ethnicity and other relevant demographics, such as socioeconomic status and occupation \cite{Mulberry2021-tc}. These models could be fit using representative serological studies with detailed cross-tabulated seropositivity estimates.”

2) I appreciated that the authors maintained an agnostic stance on the actual value of HIT (across the population & within ethnic groups) based on the results of their model. If there was available data, then it might be possible to arrive at a slightly more precise estimate by fitting the model to serial incidence data (particularly sorted by ethnic group) over time in NYC & Long Island. First, this would give some sense of R_effective. Second, if successive waves were modeled, then the shift in relative incidence & CI among these groups that is predicted in Figure 3 & Sup fig 8 may be observed in the actual data (this fits anecdotally with what I have seen in several states). Third, it may (or may not) be possible to estimate values of critical model parameters such as epsilon. It would be helpful to mention this as possible future work with the model.

Caveats about the impossibility of truly measuring HIT would still apply (due to new variants, shifting use & effective of NPIs, etc….). However, as is, the estimates of possible values for HIT are so wide as to make the underlying data used to train the model almost irrelevant. This makes the potential to leverage the model for policy decisions more limited.

We have highlighted this important limitation in the Discussion:

“Finally, we have estimated model parameters using a single cross-sectional serosurvey. To improve estimates and the ability to distinguish between model structures, future studies should use longitudinal serosurveys or case data stratified by race and ethnicity and corrected for underreporting; the challenge will be ensuring that such data are systematically collected and made publicly available, which has been a persistent barrier to research efforts \cite{Krieger2020-ss}. Addressing these data barriers will also be key for translating these and similar models into actionable policy proposals on vaccine distribution and non-pharmaceutical interventions.”

3) I think the range of R0 in the figures should be extended to go as as low as 1. Much of the pandemic in the US has been defined by local Re that varies between 0.8 & 1.2 (likely based on shifts in the degree of social distancing). I therefore think lower HIT thresholds should be considered and it would be nice to know how the extent of assortative mixing effects estimates at these lower R_e values.

We agree this would be of interest and have extended the range of R0 values. Figure 1 has been updated accordingly (see below); we also updated the text with new findings: “After fitting the models across a range of $\epsilon$ values, we observed that as $\epsilon$ increases, HITs and epidemic final sizes shifted higher back towards the homogeneous case (Figure \ref{fig:model2}, Figure 1-figure supplement 4); this effect was less pronounced for $R_0$ values close to 1.”

Figure 1: Incorporating assortativity in variable exposure models results in increased HITs across a range of $R_0$ values. Variable exposure models were fitted to NYC and Long Island serosurvey data.

4) line 274: I feel like this point needs to be considered in much more detail, either with a thoughtful discussion or with even with some simple additions to the model. How should these results make policy makers consider race and ethnicity when thinking about the key issues in the field right now such as vaccine allocation, masking, and new variants. I think to achieve the maximal impact, the authors should be very specific about how model results could impact policy making, and how we might lower the tragic discrepancies associated with COVID. If the model / data is insufficient for this purpose at this stage, then what type of data could be gathered that would allow more precise and targeted policy interventions?

We have conducted additional analyses exploring the important suggestion by the reviewers that social distancing could affect these conclusions. The text and figures have been updated accordingly:

“Finally, we assessed how robust these findings were to the impact of social distancing and other non- pharmaceutical interventions (NPIs). We modeled these mitigation measures by scaling the transmission

rate by a factor $\alpha$ beginning when 5\% cumulative incidence in the population was reached. Setting the duration of distancing to be 50 days and allowing $\alpha$ to be either 0.3 or 0.6 (i.e. a 70\% or 40\% reduction in transmission rates, respectively), we assessed how the $R_0$ versus HIT and final epidemic size relationships changed. We found that the $R_0$ versus HIT relationship was similar to in the unmitigated epidemic (Figure 1-figure supplement 5). In contrast, final epidemic sizes depended on the intensity of mitigation measures, though qualitative trends across models (e.g. increased assortativity leads to greater final sizes) remained true (Figure 1-figure supplement 6). To explore this further, we systematically varied $\alpha$ and the duration of NPIs while holding $R_0$ constant at 3. We found again that the HIT was consistent, whereas final epidemic sizes were substantially affected by the choice of mitigation parameters (Figure 1-figure supplement 7); the distribution of cumulative incidence at the point of HIT was also comparable with and without mitigation measures (Figure 2-figure supplement 8). The most stringent NPI intensities did not necessarily lead to the smallest epidemic final sizes, an idea which has been explored in studies analyzing optimal control measures \cite{Neuwirth2020- nb,Handel2007-ee}. Longitudinal changes in incidence rate ratios also were affected by NPIs, but qualitative trends in the ordering of racial and ethnic groups over time remained consistent (Figure 3- figure supplement 3).

Figure 1-figure supplement 6: Final epidemic sizes versus $R_0$ in variable exposure models with mitigation measures for $\alpha = 0.3$ (top) and $\alpha = 0.6$ (bottom). NPIs were initiated when cumulative incidence reached 5\% in all models and continued for 50 days. Models were fitted to NYC and Long Island serosurvey data.

Figure 1-figure supplement 7: Sensitivity analysis on the impact of intensity and duration of NPIs on final epidemic sizes. HIT values for the same mitigation parameters were 46.4 $\pm$ 0.5\% (range). The smallest final size, corresponding to $\alpha = 0.6$ and duration = 100, was 51\%. Census-informed assortativity models were fit to Long Island seroprevalence data. NPIs were initiated when cumulative incidence reached 5\% in all models.

See points 1 and 2 above for examples of additional data required.

Minor issues:

-This is subjective but I found the words "active" and "high activity" to describe increases in contacts per day to be confusing. I would just say more contacts per day. It might help to change "contacts" to "exposure contacts" to emphasize that not all contacts are high risk.

To clarify this, we have replaced instances of “activity level” (and similar) with “total contact rate”, indicating the total number of contacts per unit time per individual; e.g. “The estimated total contact rate ratios indicate higher contacts for minority groups such as Hispanics or Latinos and non-Hispanic Black people, which is in line with studies using cell phone mobility data \cite{Chang2020-in}; however, the magnitudes of the ratios are substantially higher than we expected given the findings from those studies.”

We have also clarified our definition of contacts: “We define contacts to be interactions between individuals that allow for transmission of SARS-CoV-2 with some non-zero probability.”

-The abstract has too much jargon for a generalist journal. I would avoid words like "proportionate mixing" & "assortative" which are very unique to modeling of infectious diseases unless they are first defined in very basic language.

We have revised the abstract to convey these same concepts in a more accessible manner: “A simple model where interactions occur proportionally to contact rates reduced the HIT, but more realistic models of preferential mixing within groups increased the threshold toward the value observed in homogeneous populations.”

-I would cite some of the STD models which have used similar matrices to capture assortative mixing.

We have added a reference in the assortative mixing section to a review of heterogeneous STD models: “Finally, under the \textit{assortative mixing} assumption, we extended this model by partitioning a fraction $\epsilon$ of contacts to be exclusively within-group and distributed the rest of the contacts according to proportionate mixing (with $\delta_{i,j}$ being an indicator variable that is 1 when $i=j$ and 0 otherwise) \cite{Hethcote1996-bf}:”

-Lines 164-5: very good point but I would add that members of ethnic / racial groups are more likely to be essential workers and also to live in multigenerational houses

We have added these helpful examples into the text: “Variable susceptibility to infection across racial and ethnic groups has been less well characterized, and observed disparities in infection rates can already be largely explained by differences in mobility and exposure \cite{Chang2020-in,Zelner2020- mb,Kissler2020-nh}, likely attributable to social factors such as structural racism that have put racial and ethnic minorities in disadvantaged positions (e.g., employment as frontline workers and residence in overcrowded, multigenerational homes) \cite{Henry_Akintobi2020-ld,Thakur2020-tw,Tai2020- ok,Khazanchi2020-xu}.”

-Line 193: "Higher than expected" -> expected by who?

We have clarified this phrase: “The estimated total contact rate ratios indicate higher exposure contacts for minority groups such as Hispanics or Latinos and non-Hispanic Black people, which is in line with studies using cell phone mobility data \cite{Chang2020-in}; however, the magnitudes of the ratios are substantially higher than we expected given the findings from those studies.”

-A limitation that needs further mention is that fact that race & ethnic group, while important, could be sub classified into strata that inform risk even more (such as SES, job type etc….)

We agree and have added this to the Discussion: “Fourth, due to data availability, we have only considered variability in exposure due to one demographic characteristic; models should ideally strive to also account for the effects of age on susceptibility and exposure within strata of race and ethnicity and other relevant demographics, such as socioeconomic status and occupation \cite{Mulberry2021-tc}. These models could be fit using representative serological studies with detailed cross-tabulated seropositivity estimates.”

Reviewer #2 (Public Review):

Overall I think this is a solid and interesting piece that is an important contribution to the literature on COVID-19 disparities, even if it does have some limitations. To this point, most models of SARS-CoV-2 have not included the impact of residential and occupational segregation on differential group-specific covid outcomes. So, the authors are to commended on their rigorous and useful contribution on this valuable topic. I have a few specific questions and concerns, outlined below:

We thank the reviewer for the supportive comments.

1) Does the reliance on serosurvey data collected in public places imply a potential issue with left-censoring, i.e. by not capturing individuals who had died? Can the authors address how survival bias might impact their results? I imagine this could bring the seroprevalence among older people down in a way that could bias their transmission rate estimates.

We have included this important point in the limitations section on potential serosurvey biases: “First, biases in the serosurvey sampling process can substantially affect downstream results; any conclusions drawn depend heavily on the degree to which serosurvey design and post-survey adjustments yield representative samples \cite{Clapham2020-rt}. For instance, because the serosurvey we relied on primarily sampled people at grocery stores, there is both survival bias (cumulative incidence estimates do not account for people who have died) and ascertainment bias (undersampling of at-risk populations that are more likely to self-isolate, such as the elderly) \cite{Rosenberg2020-qw,Accorsi2021-hx}. These biases could affect model estimates if, for instance, the capacity to self-isolate varies by race or ethnicity -- as suggested by associations of neighborhood-level mobility versus demographics \cite{Kishore2020- sy,Kissler2020-nh} -- leading to an overestimate of cumulative incidence and contact rates in whites.”

2) It might be helpful to think in terms of disparities in HITs as well as disparities in contact rates, since the HIT of whites is necessarily dependent on that of Blacks. I'm not really disagreeing with the thrust of what their analysis suggests or even the factual interpretation of it. But I do think it is important to phrase some of the conclusions of the model in ways that are more directly relevant to health equity, i.e. how much infection/vaccination coverage does each group need for members of that group to benefit from indirect protection?

We agree with this important point and indeed this was the goal, in part, of the analyses in Figure 2. We have added additional text to the Discussion highlighting this: “Projecting the epidemic forward indicated that the overall HIT was reached after cumulative incidence had increased disproportionately in minority groups, highlighting the fundamentally inequitable outcome of achieving herd immunity through infection. All of these factors underscore the fact that incorporating heterogeneity in models in a mechanism-free manner can conceal the disparities that underlie changes in epidemic final sizes and HITs. In particular, overall lower HIT and final sizes occur because certain groups suffer not only more infection than average, but more infection than under a homogeneous mixing model; incorporating heterogeneity lowers the HIT but increases it for the highest-risk groups (Figure \ref{fig:hitcomp}).”

For vaccination, see our response to Reviewer #1 point 4.

3) The authors rely on a modified interaction index parameterized directly from their data. It would be helpful if they could explain why they did not rely on any sources of mobility data. Are these just not broken down along the type of race/ethnicity categories that would be necessary to complete this analysis? Integrating some sort of external information on mobility would definitely strengthen the analysis.

This is a great suggestion, but this type of data has generally not been available due to privacy concerns from disaggregating mobility data by race and ethnicity (Kishore et al., 2020). Instead, we modeled NPIs as mentioned in Reviewer #1 point 4, with the caveat that reduction in mobility was assumed to be identical across groups. We added this into the text explicitly as a limitation: “Third, we have assumed the impact of non-pharmaceutical interventions such as stay-at-home policies, closures, and the like to equally affect racial and ethnic groups. Empirical evidence suggests that during periods of lockdown, certain neighborhoods that are disproportionately wealthy and white tend to show greater declines in mobility than others \cite{Kishore2020-sy,Kissler2020-nh}. These simplifying assumptions were made to aid in illustrating the key findings of this model, but for more detailed predictive models, the extent to which activity level differences change could be evaluated using longitudinal contact survey data \cite{Feehan2020-ta}, since granular mobility data are typically not stratified by race and ethnicity due to privacy concerns \cite{Kishore2020-mg}.”

Reviewer #3 (Public Review):

Ma et al investigate the effect of racial and ethnic differences in SARS-CoV-2 infection risk on the herd immunity threshold of each group. Using New York City and Long Island as model settings, they construct a race/ethnicity-structured SEIR model. Differential risk between racial and ethnic groups was parameterized by fitting each model to local seroprevalence data stratified demographically. The authors find that when herd immunity is reached, cumulative incidence varies by more than two fold between ethnic groups, at approximately 75% of Hispanics or Latinos and only 30% of non-Hispanic Whites.

This result was robust to changing assumptions about the source of racial and ethnic disparities. The authors considered differences in disease susceptibility, exposure levels, as well as a census-driven model of assortative mixing. These results show the fundamentally inequitable outcome of achieving herd immunity in an unmitigated epidemic.

The authors have only considered an unmitigated epidemic, without any social distancing, quarantine, masking, or vaccination. If herd immunity is achieved via one of these methods, particularly vaccination, the disparities may be mitigated somewhat but still exist. This will be an important question for epidemiologists and public health officials to consider throughout the vaccine rollout.

We thank the reviewer for the detailed and helpful summary and suggestions.

Author Response

Summary: A major tenet of plant pathogen effector biology has been that effectors from very different pathogens converge on a small number of host targets with central roles in plant immunity. The current work reports that effectors from two very different pathogens, an insect and an oomycete, interact with the same plant protein, SIZ1, previously shown to have a role in plant immunity. Unfortunately, apart from some technical concerns regarding the strength of the data that the effectors and SIZ1 interact in plants, a major limitation of the work is that it is not demonstrated that the effectors alter SIZ1 activity in a meaningful way, nor that SIZ1 is specifically required for action of the effects.

We thank the editor and reviewers for their time to review our manuscript and their helpful and constructive comments. The reviews have helped us focus our attention on additional experiments to test the hypothesis that effectors Mp64 (from an aphid) and CRN83-152 (from an oomycete) indeed alter SIZ1 activity or function. We have revised our manuscript and added the following data:

1) Mp64, but not CRN83-152, stabilizes SIZ1 in planta. (Figure 1 in the revised manuscript).

2) AtSIZ1 ectopic expression in Nicotiana benthamiana triggers cell death from 3-4 days after agroinfiltration. Interestingly CRN83-152_6D10 (a mutant of CRN83-152 that has no cell death activity), but not Mp64, enhances the cell death triggered by AtSIZ1 (Figure 2 in the revised manuscript).

For 1) we have added the following panel to Figure 1 as well as three biological replicates of the stabilisation assays in the Supplementary data (Fig S3):

Figure 1 panel C. Stabilisation of SIZ1 by Mp64. Western blot analyses of protein extracts from agroinfiltrated leaves expressing combinations of GFP-GUS, GFP Mp64 and GFP-CRN83_152_6D10 with AtSIZ1-myc or NbSIZ1-myc. Protein size markers are indicated in kD, and equal protein amounts upon transfer is shown upon ponceau staining (PS) of membranes. Blot is representative of three biological replicates , which are all shown in supplementary Fig. S3. The selected panels shown here are cropped from Rep 1 in supplementary Fig. S3.

For 2) we have added the folllowing new figure (Fig. 2 in the revised manuscript):

Fig. 2. SIZ1-triggered cell death in N. benthamiana is enhanced by CRN83_152_6D10 but not Mp64. (A) Scoring overview of infiltration sites for SIZ1 triggered cell death. Infiltration site were scored for no symptoms (score 0), chlorosis with localized cell death (score 1), less than 50% of the site showing visible cell death (score 2), more than 50% of the site showing cell death (score 3). (B) Bar graph showing the proportions of infiltration sites showing different levels of cell death upon expression of AtSIZ1, NbSIZ1 (both with a C-terminal RFP tag) and an RFP control. Graph represents data from a combination of 3 biological replicates of 11-12 infiltration sites per experiment (n=35). (C) Bar graph showing the proportions of infiltration sites showing different levels of cell death upon expression of SIZ1 (with C-terminal RFP tag) either alone or in combination with aphid effector Mp64 or Phytophthora capsica effector CRN83_152_6D10 (both effectors with GFP tag), or a GFP control. Graph represent data from a combination of 3 biological replicates of 11-12 infiltration sites per experiment (n=35).

Our new data provide further evidence that SIZ1 function is affected by effectors Mp64 (aphid) and CRN83-152 (oomycete), and that SIZ1 likely is a vital virulence target. Our latest results also provide further support for distinct effector activities towards SIZ1 and its variants in other species. SIZ1 is a key immune regulator to biotic stresses (aphids, oomycetes, bacteria and nematodes), on which distinct virulence strategies seem to converge. The mechanism(s) underlying the stabilisation of SIZ1 by Mp64 is yet unclear. However, we hypothesize that increased stability of SIZ1, which functions as an E3 SUMO ligase, leads to increased SUMOylation activity towards its substrates. We surmise that SIZ1 complex formation with other key regulators of plant immunity may underpin these changes. Whether the cell death, triggered by AtSIZ1 upon transient expression in Nicotiana benthamiana, is linked to E3 SUMO ligase activity remains to be investigated. Expression of AtSIZ1 in a plant species other than Arabidopsis may lead to mistargeting of substrates, and subsequent activation of cell death. Dissecting the mechanistic basis of SIZ1 targeting by distinct pathogens and pests will be an important next step in addressing these hypotheses towards understanding plant immunity.

Reviewer #1:

In this manuscript, the authors suggest that SIZ1, an E3 SUMO ligase, is the target of both an aphid effector (Mp64 form M. persicae) and an oomycete effector (CRN83_152 from Phytophthora capsica), based on interaction between SIZ1 and the two effectors in yeast, co-IP from plant cells and colocalization in the nucleus of plant cells. To support their proposal, the authors investigate the effects of SIZ1 inactivation on resistance to aphids and oomycetes in Arabidopsis and N. benthamiana. Surprisingly, resistance is enhanced, which would suggest that the two effectors increase SIZ1 activity.

Unfortunately, not only do we not learn how the effectors might alter SIZ1 activity, there is also no formal demonstration that the effects of the effectors are mediated by SIZ1, such as investigating the effects of Mp64 overexpression in a siz1 mutant. We note, however, that even this experiment might not be entirely conclusive, since SIZ1 is known to regulate many processes, including immunity. Specifically, siz1 mutants present autoimmune phenotype, and general activation of immunity might be sufficient to attenuate the enhanced aphid susceptibility seen in Mp64 overexpressers.

To demonstrate unambiguously that SIZ1 is a bona fide target of Mp64 and CRN83_152 would require assays that demonstrate either enhanced SIZ1 accumulation or altered SIZ1 activity in the presence of Mp64 and CRN83_152.

The enhanced resistance upon knock-down/out of SIZ1 suggests pathogen and pest susceptibility requires SIZ1. We hypothesize that the effectors either enhance SIZ1 activity or that the effectors alter SIZ1 specificity towards substrates rather than enzyme activity itself. To investigate how effectors coopt SIZ1 function would require a comprehensive set of approaches and will be part of our future work. While we agree that this aspect requires further investigation, we think the proposed experiments go beyond the scope of this study.

After receiving reviewer comments, including on the quality of Figure 1, which shows western blots of co-immunoprecipitation experiments, we re-analyzed independent replicates of effector-SIZ1 coexpression/ co-immunoprecipitation experiments. The reviewer rightly pointed out that in the presence of Mp64, SIZ1 protein levels increase when compared to samples in which either the vector control or CRN83-152_6D10 are co-infiltrated. Through carefully designed experiments, we can now affirm that Mp64 co-expression leads to increased SIZ1 protein levels (Figure 1C and Supplementary Figure S3, revised manuscript). Our results offer both an explanation of different SIZ1 levels in the input samples (original submission, Figure 1A/B) as well as tantalizing new clues to the nature of distinct effector activities.

Besides, we were able to confirm a previous preliminary finding not included in the original submission that ectopic expression of AtSIZ1 in Nicotiana benthamiana triggers cell death (3/4 days after infiltration) and that CRN83-152_6D10 (which itself does not trigger cell death) enhances this phenotype.

We have considered overexpression of Mp64 in the siz1 mutant, but share the view that the outcome of such experiments will be far from conclusive.

In summary, we have added new data that further support that SIZ1 is a bonafide target of Mp64 and CRN83-152 (i.e. increased accumulation of SIZ1 in the presence of Mp64, and enhanced SIZ cell death activation in the presence of CRN83-152_6D10).

Reviewer #2:

The study provides evidence that an aphid effector Mp64 and a Phytophthora capsici effector CRN83_152 can both interact with the SIZ1 E3 SUMO-ligase. The authors further show that overexpression of Mp64 in Arabidopsis can enhance susceptibility to aphids and that a loss-of-function mutation in Arabidopsis SIZ1 or silencing of SIZ1 in N. benthamiana plants lead to increased resistance to aphids and P. capsici. On siz1 plants the aphids show altered feeding patterns on phloem, suggestive of increased phloem resistance. While the finding is potentially interesting, the experiments are preliminary and the main conclusions are not supported by the data.

Specific comments:

The suggestion that SIZ1 is a virulence target is an overstatement. Preferable would be knockouts of effector genes in the aphid or oomycete, but even with transgenic overexpression approaches, there are no direct data that the biological function of the effectors requires SIZ1. For example, is SIZ1 required for the enhanced susceptibility to aphid infestation seen when Mp64 is overexpressed? Or does overexpression of SIZ1 enhance Mp64-mediated susceptibility?

What do the effectors do to SIZ1? Do they alter SUMO-ligase activity? Or are perhaps the effectors SUMOylated by SIZ1, changing effector activity?

We agree that having effector gene knock-outs in aphids and oomycetes would be ideal for dissecting effector mediated targeting of SIZ1. Unfortunately, there is no gene knock-out system established in Myzus persicae (our aphid of interest), and CAS9 mediated knock-out of genes in Phytophthora capsici has not been successful in our lab as yet, despite published reports. Moreover, repeated attempts to silence Mp64, other effector and non-effector coding genes, in aphids (both in planta and in vitro) have not been successful thus far, in our hands. As detailed in our response to Reviewer 1, we considered the use of transgenic approaches not appropriate as data interpretation would become muddied by the strong immunity phenotype seen in the siz1-2 mutant.

As stated before, we hypothesize that the effectors either enhance SIZ1 activity or alter SIZ1 substrate specificity. Mp64-induced accumulation of SIZ1 could form the basis of an increase in overall SIZ1 activity. This hypothesis, however, requires testing. The same applies to the enhanced SIZ1 cell death activation in the presence of CRN83-152_6D10.

Whilst our new data support our hypothesis that effectors Mp64 and CRN83-152 affect SIZ1 function, how exactly these effectors trigger susceptibility, requires significant work. Given the substantial effort needed and the research questions involved, we argue that findings emanating from such experiments warrant standalone publication.

While stable transgenic Mp64 overexpressing lines in Arabidopsis showed increased susceptibility to aphids, transient overexpression of Mp64 in N. benthamiana plants did not affect P. capsici susceptibility. The authors conclude that while the aphid and P. capsici effectors both target SIZ1, their activities are distinct. However, not only is it difficult to compare transient expression experiments in N. benthamiana with stable transgenic Arabidopsis plants, but without knowing whether Mp64 has the same effects on SIZ1 in both systems, to claim a difference in activities remains speculative.

We agree that we cannot compare effector activities between different plant species. We carefully considered every statement regarding results obtained on SIZ1 in Arabidopsis and Nicotiana benthamiana. We can, however, compare activities of the two effectors when expressed side by side in the same plant species. In our original submission, we show that expression of CRN83 152 but not Mp64 in Nicotiana benthamiana enhances susceptibility to Phytophthora capsici. In our revised manuscript, we present new data showing distinct effector activities towards SIZ1 with regards to 1) enhanced SIZ1 stability and 2) enhanced SIZ1 triggered cell death. These findings raise questions as to how enhanced SIZ1 stability and cell death activation is relevant to immunity. We aim to address these critical questions by addressing the mechanistic basis of effector-SIZ1 interactions.

The authors emphasize that the increased resistance to aphids and P. capsici in siz1 mutants or SIZ1 silenced plants are independent of SA. This seems to contradict the evidence from the NahG experiments. In Fig. 5B, the effects of siz1 are suppressed by NahG, indicating that the resistance seen in siz1 plants is completely dependent on SA. In Fig 5A, the effects of siz1 are not completely suppressed by NahG, but greatly attenuated. It has been shown before that SIZ1 acts only partly through SNC1, and the results from the double mutant analyses might simply indicate redundancy, also for the combinations with eds1 and pad4 mutants.

We emphasized that siz1-2 increased resistance to aphids is independent of SA, which is supported by our data (Figure 5A). Still, we did not conclude that the same applies to increased resistance to Phytophthora capsici (Figure 5B). In contrast, the siz1-2 enhanced resistance to P. capsici appears entirely dependent on SA levels, with the level of infection on the siz1-2/NahG mutants even slightly higher than on the NahG line and Col-0 plants. We exercise caution in the interpretation of this data given the significant impact SA signalling appears to have on Phytophthora capsici infection.

The reviewer commented on the potential for functional redundancy in the siz1-2 double mutants. Unfortunately, we are unsure what redundancy s/he is referring to. SNC1, EDS1, and PAD4 all are components required for immunity, and their removal from the immune signalling network (using the mutations in the lines we used here) impairs immunity to various plant pathogens. The siz1-2 snc1-11, siz1-2 eds1-2, and siz1-2 pad4-1 double mutants have similar levels of susceptibility to the bacterial pathogen Pseudomonas syringae when compared to the corresponding snc1-11, eds1-2 and pad4-1 controls (at 22oC). These previous observations indicate that siz1 enhanced resistance is dependent on these signalling components (Hammoudi et al., 2018, Plos Genetics).

In contrast to this, we observed a strong siz1 enhanced resistance phenotype in the absence of snc1- 11, eds1 2 and pad4-1. Notably, the siz1-2 snc1-11 mutant does not appear immuno-compromised when compared to siz1-2 in fecundity assays, indicating that the siz1-2 phenotype is independent of SNC1. In our view, these data suggest that signalling components/pathways other than those mediated by SNC1, EDS1, and PAD4 are involved. We consider this to be an exciting finding as our data points to an as of yet unknown SIZ1-dependent signalling pathway that governs immunity to aphids.

How do NahG or Mp64 overexpression affect aphid phloem ingestion? Is it the opposite of the behavior on siz1 mutants?

We have not performed further EPG experiments on additional transgenic lines used in the aphid assay. These experiments are quite challenging and time consuming. Moreover, accommodating an experimental set-up that allows us to compare multiple lines at the same time is not straightforward. Considering that NahG did not affect aphid performance (Figure 5A), we do not expect to see an effect on phloem ingestion.

Author Response

1) Please comment on why many of the June samples failed to provide sufficient sequence information, especially since not all of them had low yields (supp table 2 and supp figure 5).

An extended paragraph about experimental intricacies of our study has been added to the Discussion. It has also been also slightly restructured to give a better and wider overview of how future freshwater monitoring studies using nanopore sequencing can be improved (page 18, lines 343-359).

We wish to highlight that all three MinION sequencing runs here analysed feature substantially higher data throughput than that of any other recent environmental 16S rRNA sequencing study with nanopore technology, as recently reviewed by Latorre-Pérez et al. (Biology Methods and Protocols 2020, doi:10.1093/biomethods/bpaa016). One of this work's sequencing runs has resulted in lower read numbers for water samples collected in June 2018 (~0.7 Million), in comparison to the ones collected in April and August 2018 (~2.1 and ~5.5 Million, respectively). While log-scale variabilities between MinION flow cell throughput have been widely reported for both 16S and shotgun metagenomics approaches (e.g. see Latorre-Pérez et al.), the count of barcode-specific 16S reads is nevertheless expected to be correlated with the barcode-specific amount of input DNA within a given sequencing run. As displayed in Supplementary Figure 7b, we see a positive, possibly logarithmic trend between the DNA concentration after 16S rDNA amplification and number of reads obtained. With few exceptions (April-6, April-9.1 and Apri-9.2), we find that sample pooling with original 16S rDNA concentrations of ≳4 ng/µl also results in the surpassing of the here-set (conservative) minimum read threshold of 37,000 for further analyses. Conversely, all June samples that failed to reach 37,000 reads did not pass the input concentration of 4 ng/µl, despite our attempt to balance their quantity during multiplexing.

We reason that such skews in the final barcode-specific read distribution would mainly arise from small concentration measurement errors, which undergo subsequent amplification during the upscaling with comparably large sample volume pipetting. While this can be compensated for by high overall flow cell throughput (e.g. see August-2, August-9.1, August-9.2), we think that future studies with much higher barcode numbers can circumvent this challenge by leveraging an exciting software solution: real-time selective sequencing via “Read Until”, as developed by Loose et al. (Nature Methods 2016, doi:10.1038/nmeth.3930). In the envisaged framework, incoming 16S read signals would be in situ screened for the sample-barcode which in our workflow is PCR-added to both the 5' and 3' end of each amplicon. Overrepresented barcodes would then be counterbalanced by targeted voltage inversion and pore "rejection" of such reads, until an even balance is reached. Lately, such methods have been computationally optimised, both through the usage of GPUs (Payne et al., bioRxiv 2020, https://doi.org/10.1101/2020.02.03.926956) and raw electrical signals (Kovaka et al., bioRxiv 2020, https://doi.org/10.1101/2020.02.03.931923).

2) It would be helpful if the authors could mention the amount (or proportion) of their sequenced 16S amplicons that provided species-level identification, since this is one of the advantages of nanopore sequencing.

We wish to emphasize that we intentionally refrained from reporting the proportion of 16S rRNA reads that could be classified at species level, since we are wary of any automated species level assignments even if the full-length 16S rRNA gene is being sequenced. While we list the reasons for this below, we appreciate the interest in the theoretical proportion of reads at species level assignment. We therefore re-analyzed our dataset, and now also provide the ratio of reads that could be classified at species level using Minimap2 (pages 16-17, lines 308-314).

To this end, we classified reads at species level if the species entry of the respective SILVA v.132 taxonomic ID was either not empty, or neither uncultured bacterium nor metagenome. Therefore, many unspecified classifications such as uncultured species of some bacterial genus are counted as species-level classifications, rendering our approach lenient towards a higher ratio of species level classifications. Still, the species level classification ratios remain low, on average at 16.2 % across all included river samples (genus-level: 65.6 %, family level: 76.6 %). The mock community, on the other hand, had a much higher species classification rate (>80 % in all three replicates), which is expected for a well-defined, well-referenced and divergent composition of only eight bacterial taxa, and thus re-validates our overall classification workflow.

On a theoretical level, we mainly refrain from automated across-the-board species level assignments because: (1) many species might differ by very few nucleotide differences within the 16S amplicon; distinguishing these from nanopore sequencing errors (here ~8 %) remains challenging (2) reference databases are incomplete and biased with respect to species level resolution, especially regarding certain environmental contexts; it is likely that species assignments would be guided by references available from more thoroughly studied niches than freshwater

Other recent studies have also shown that across-the-board species-level classification is not yet feasible with 16S nanopore sequencing, for example in comparison with Illumina data (Acharya et al., Scientific Reports 2019, doi:10.25405/data.ncl.9693533) which showed that “more reliable information can be obtained at genus and family level”, or in comparison with longer 16S-ITS-23S amplicons (Cusco et al., F1000Research 2019, doi: 10.12688/f1000research.16817.2), which “remarkably improved the taxonomy assignment at the species level”.

3) It is not entirely clear how the authors define their core microbiome. Are they reporting mainly the most abundant taxa (dominant core microbiome), and would this change if you look at a taxonomic rank below the family level? How does the core compare, for example, with other studies of this same river?

The here-presented core microbiome indeed represents the most abundant taxa, with relatively consistent profiles between samples. We used hierarchical clustering (Figure 4a, C2 and C4) on the bacterial family level, together with relative abundance to identify candidate taxa. Filtering these for median abundance > 0.1% across all samples resulted in 27 core microbiome families. To clarify this for the reader, we have added a new paragraph to the Material and Methods (section 2.7; page 29, lines 653-658).

We have also performed the same analysis on the bacterial genus level and now display the top 27 most abundant genera (median abundance > 0.2%), together with their corresponding families and hierarchical clustering analysis in a new Supplementary Figure 4. Overall, high robustness is observed with respect to the families of the core microbiome: out of the top 16 core families (Figure 4b), only the NS11-12 marine group family is not represented by the top 27 most abundant genera (Supplementary Figure 4b). We reason that this is likely because its corresponding genera are composed of relatively poorly resolved references of uncultured bacteria, which could thus not be further classified.

To the best of our knowledge, there are only two other reports that feature metagenomic data of the River Cam and its wastewater influx sources (Rowe et al., Water Science & Technology 2016, doi:10.2166/wst.2015.634; Rowe et al., Journal of Antimicrobial Chemotherapy 2017, doi:10.1093/jac/dkx017). While both of these primarily focus on the diversity and abundance of antimicrobial resistance genes using Illumina shotgun sequencing, they only provide limited taxonomic resolution on the river's core microbiome. Nonetheless, Rowe et al. (2016) specifically highlighted Sphingobium as the most abundant genus in a source location of the river (Ashwell, Hertfordshire). This genus belongs to the family of Sphingomonadaceae, which is also among the five most dominant families identified in our dataset. It thus forms part of what we define as the core microbiome of the River Cam (Figure 4b), and we have therefore highlighted this consistency in our manuscript's Discussion (page 17, lines 316-319).

4) Please consider revising the amount of information in some of the figures (such as figure 2 and figure 3). The resulting images are tiny, the legends become lengthy and the overall impact is reduced. Consider splitting these or moving some information to the supplements.

To follow this advice, we have split Figure 2 into two less compact figures. We have moved more detailed analyses of our classification tool benchmark to the supplement (now Supplementary Figure 1). Supplementary Figure 1 notably also contains a new summary of the systematic computational performance measurements of each classification tool (see minor suggestions).

Moreover, we here suggest that the original Figure 3 may be divided into two figures: one to visualise the sequencing output, data downsampling and distribution of the most abundant families (now Figure 3), and the other featuring the clustering of bacterial families and associated core microbiome (now Figure 4). We think that both the data summary and clustering/core microbiome analyses are of particular interest to the reader, and that they should be kept as part of the main analyses rather than the supplement – however, we are certainly happy to discuss alternative ideas with the reviewers and editors.

5) Given that the authors claim to provide a simple, fast and optimized workflow it would be good to mention how this workflow differs or provides faster and better analysis than previous work using amplicon sequencing with a MinION sequencer.

Data throughput, sequencing error rates and flow cell stability have seen rapid improvements since the commercial release of MinION in 2015. In consequence, bioinformatics community standards regarding raw data processing and integration steps are still lacking, as illustrated by a thorough recent benchmark of fast5 to fastq format "basecalling" methods (Wick et al., Genome Biology 2019, doi: 10.1186/s13059-019-1727-y).

Early on during our analyses, we noticed that a plethora of bespoke pipelines have been reported in recent 16S environmental surveys using MinION (e.g. Kerkhof et al., Microbiome 2017, 10.1186/s40168-017-0336-9; Cusco et al., F1000 Research 2018, 10.12688/f1000research.16817.2; Acharya et al., Scientific Reports 2019, 10.1038/s41598-019-51997-x; Nygaard et al., Scientific Reports 2020, doi: 10.1038/s41598-020-59771-0). This underlines a need for more unified bioinformatics standards of (full-length) 16S amplicon data treatment, while similar benchmarks exist for short-read 16S metagenomics approaches, as well as for nanopore shotgun sequencing (e.g. Ye et al., Cell 2019, doi: 10.1016/j.cell.2019.07.010; Latorre-Pérez et al., Scientific Reports 2020, doi:10.1038/s41598-020-70491-3).

By adding a thorough speed and memory usage summary (new Supplementary Figure 1b), in addition to our (mis)classification performance tests based on both mock and complex microbial community analyses, we provide the reader with a broad overview of existing options. While the widely used Kraken 2 and Centrifuge methods provide exceptional speed, we find that this comes with a noticeable tradeoff in taxonomic assignment accuracy. We reason that Minimap2 alignments provide a solid compromise between speed and classification performance, with the MAPseq software offering a viable alternative should memory usage limitation apply to users.

We intend to extend this benchmarking process to future tools, and to update it on our GitHub page (https://github.com/d-j-k/puntseq). This page notably also hosts a range of easy-to-use scripts for employing downstream 16S analysis and visualization approaches, including ordination, clustering and alignment tests.

The revised Discussion now emphasises the specific advancements of our study with respect to freshwater analysis and more general standardisation of nanopore 16S sequencing, also in contrast to previous amplicon nanopore sequencing approaches in which only one or two bioinformatics workflows were tested (page 16, lines 297-306).

They also mention that nanopore sequencing is an "inexpensive, easily adaptable and scalable framework" The term "inexpensive" doesn't seem appropriate since it is relative. In addition, they should also discuss that although it is technically convenient in some aspects compared to other sequencers, there are still protocol steps that need certain reagents and equipment that is similar or the same to those needed for other sequencing platforms. Common bottlenecks such as DNA extraction methods, sample preservation and the presence of inhibitory compounds should be mentioned.

We agree with the reviewers that “inexpensive” is indeed a relative term, which needs further clarification. We therefore now state that this approach is “cost-effective” and discuss future developments such as the 96-sample barcoding kits and Flongle flow cells for small-scale water diagnostics applications, which will arguably render lower per-sample analysis costs in the future (page 18, lines 361-365).

Other investigators (e.g. Boykin et al., Genes 2019, doi:10.3390/genes10090632; Acharya et al., Water Technology 2020, doi:10.1016/j.watres.2020.116112) have recently shown that the full application of DNA extraction and in-field nanopore sequencing can be achieved at comparably low expense: Boykin et al. studied cassava plant pathogens using barcoded nanopore shotgun sequencing, and estimated costs of ~45 USD per sample, while we calculate ~100 USD per sample in this study. Acharya et al. undertook in situ water monitoring between Birtley, UK and Addis Ababa, Ethiopia, estimated ~75-150 USD per sample and purchased all necessary equipment for ~10,000 GBP – again, we think that this lies roughly within a similar range as our (local) study's total cost of ~3,670 GBP (Supplementary Table 6).

The revised manuscript now mentions the possibility of increasing sequencing yield by improving DNA extraction methods, by taking sample storage and potential inhibitory compounds into account in the planning phase (page 18, lines 348-352).

Minor points:

-Please include a reference to the statement saying that the river Cam is notorious for the "infections such as leptospirosis".

There are indeed several media reports that link leptospirosis risk to the local River Cam (e.g. https://www.cambridge-news.co.uk/news/cambridge-news/weils-disease-river-cam-leptosirosis-14919008 or https://www.bbc.com/news/uk-england-cambridgeshire-29060018). As we, however, did not find a scientific source for this information, we have slightly adjusted the statement in our manuscript from referring to Cambridge to instead referring to the entire United Kingdom. Accordingly, we now cite two reports from Public Health England (PHE) about serial leptospirosis prevalence in the United Kingdom (page 13, lines 226-227).

-Please check figure 7 for consistency across panels, such as shading in violet and labels on the figures that do not seem to correspond with what is stated in the legend. Please mention what the numbers correspond to in outer ring. Check legend, where it says genes is probably genus.

Thank you for pointing this out. We have revised (now labelled) Figure 8 and removed all inconsistencies between the panels. The legend has also been updated, which now includes a description of the number labelling of the tree, and a clearer differentiation between the colour coding of the tree nodes and the background highlighting of individual nanopore reads.

-Page 6. There is a "data not shown" comment in the text: "Benchmarking of the classification tools on one aquatic sample further confirmed Minimap2's reliable performance in a complex bacterial community, although other tools such as SPINGO (Allard, Ryan, Jeffery, & Claesson, 2015), MAPseq (Matias Rodrigues, Schmidt, Tackmann, & von Mering, 2017), or IDTAXA (Murali et al., 2018) also produced highly concordant results despite variations in speed and memory usage (data not shown)." There appears to be no good reason that this data is not shown. In case the speed and memory usage was not recorded, is advisable to rerun the analysis and quantify these variables, rather than mentioning them and not reporting them. Otherwise, provide an explanation for not showing the data please.

This is a valid point, and we agree with the reviewers that it is worth properly following up on this initial observation. To this end, our revised manuscript now entails a systematic characterisation of the twelve tools' runtime and memory usage performance. This has been added as Supplementary Figure 1b and under the new Materials and Methods section 2.2.4 (page 26, lines 556-562), while the corresponding results and their implications are discussed on page 16, lines 301-306. Particularly with respect to the runtime measurements, it is worth noting that these can differ by several orders of magnitude between the classifiers, thus providing an additional clarification on our choice of the - relatively fast - Minimap2 alignments.

-In Figure 4, it would be important to calculate if the family PCA component contribution differences in time are differentially significant. In Panel B, depicted is the most evident variance difference but what about other taxa which might not be very abundant but differ in time? One can use the fitFeatureModel function from the metagenomeSeq R library and a P-adjusted threshold value of 0.05, to validate abundance differences in addition to your analysis.

To assess if the PC component contribution of Figure 5 (previously Figure 4) significantly differed between the three time points, we have applied non-parametric tests to all season-grouped samples except for the mock community controls. We first applied Kruskal-Wallis H-test for independent samples, followed by post-hoc comparisons using two-sided Mann-Whitney U rank tests.

The Kruskal-Wallis test established a significant difference in PC component contributions between the three time points (p = 0.0049), with most of the difference stemming from divergence between April and August samples according to the post-hoc tests (p = 0.0022). The June sampled seemed to be more similar to the August ones (p = 0.66) than to the ones from April (p = 0.11), recapitulating the results of our hierarchical clustering analysis (Figure 4a).

We have followed the reviewers' advice and applied a complementary approach, using the fitFeatureModel of metagenomeSeq to fit a zero-inflated log-normal mixture model of each bacterial taxon against the time points. As only three independent variables can be accounted for by the model (including the intercept), we have chosen to investigate the difference between the spring (April) and summer (June, August) months to capture the previously identified difference between these months. At a nominal P-value threshold of 0.05, this analysis identifies seven families to significantly differ in their relative composition between spring and summer, namely Cyanobiaceae, Armatimonadaceae, Listeriaceae, Carnobacteriaceae, Azospirillaceae, Cryomorphaceae, and Microbacteriaceae. Three out of these seven families were also detected by the PCA component analysis (Carnobacteriacaea, Azospirillaceae, Microbacteriaceae) and two more (Listeriacaea, Armatimonadaceae) occured in the top 15 % of that analysis (out of 357 families).

This approach represents a useful validation of our principal component analysis' capture of likely seasonal divergence, but moreover allows for a direct assessment of differential bacterial composition across time points. We have therefore integrated the analysis into our manuscript (page 10, lines 184-186; Materials and Methods section 2.6, page 29, lines 641-647) – thank you again for this suggestion.

-Page 12-13. In the paragraph: "Using multiple sequence alignments between nanopore reads and pathogenic species references, we further resolved the phylogenies of three common potentially pathogenic genera occurring in our river samples, Legionella, Salmonella and Pseudomonas (Figure 7a-c; Material and Methods). While Legionella and Salmonella diversities presented negligible levels of known harmful species, a cluster of reads in downstream sections indicated a low abundance of the opportunistic, environmental pathogen Pseudomonas aeruginosa (Figure 7c). We also found significant variations in relative abundances of the Leptospira genus, which was recently described to be enriched in wastewater effluents in Germany (Numberger et al., 2019) (Figure 7d)."

Here it is important to mention the relative abundance in the sample. While no further experiments are needed, the authors should mention and discuss that the presence of DNA from pathogens in the sample has to be confirmed by other microbiology methodologies, to validate if there are viable organisms. Definitively, it is a big warning finding pathogen's DNA but also, since it is characterized only at genus level, further investigation using whole metagenome shotgun sequencing or isolation, would be important.

We agree that further microbiological assays, particularly target-specific species isolation and culturing, would be essential to validate the presence of living pathogenic bacteria. Accordingly, our revised Discussion now contains a paragraph that encourages such experiments as part of the design of future studies (with a fully-equipped laboratory infrastructure); page 17, 338-341.

-Page 15: "This might help to establish this family as an indicator for bacterial community shifts along with water temperature fluctuations."

Temperature might not be the main factor for the shift. There could be other factors that were not measured that could contribute to this shift. There are several parameters that are not measured and are related to water quality (COD, organic matter, PO4, etc).

We agree that this was a simplified statement, given our currently limited number of samples, and have therefore slightly expanded on this point (page 17, lines 323-325). It is indeed possible that differential Carnobacteriaceae abundances between the time point measurements may have arisen not as a consequence of temperature fluctuations (alone), but instead as a consequence of the observed hydrochemical changes like e.g. Ca2+, Mg2+, HCO3- (Figure 6b-c) or possible even water flow speed reductions (Supplementary Figure 6d).

-"A number of experimental intricacies should be addressed towards future nanopore freshwater sequencing studies with our approach, mostly by scrutinising water DNA extraction yields, PCR biases and molar imbalances in barcode multiplexing (Figure 3a; Supplementary Figure 5)."

Here you could elaborate more on the challenges, as mentioned previously.

We realise that we had not discussed the challenges in enough detail, and the Discussion now contains a substantially more detailed description of these intricacies (page 18, lines 343-359).

Author Response

Reviewer #1:

Summary:

In this paper, the authors utilize CRISPR-Cas9 to generate two different DMD cell lines. The first is a DMD human myoblast cell line that lacks exon 52 within the dystrophin gene. The second is a DMD patient cell line that is missing miRNA binding sites within the regulatory regions of the utrophin gene, resulting in increased utrophin expression. Then, the authors proceeded to test antisense oligonucleotides and utrophin up-regulators in these cell lines.

Overall opinion (expanded in more detail below).

The paper suffers from the following weaknesses:

1) The protocol used to generate the myoblast cell lines is rather inefficient and is not new.

2) Many of the data figures are of low quality and are missing proper controls (detailed in points 5,7,10, 12, 13,14)

Detailed critiques:

1) The title needs to be changed. The method used by the authors is inefficient. The title should instead focus on the two cell lines generated.

We appreciate the reviewer’s comments: thanks to them, we have realized the focus of the manuscript should be in the new models we described and less in the methodology used to create them.

Originally, we wanted to share the problems we faced when applying new CRISPR/Cas9 edition techniques to myoblasts: our conversations with other researchers in the field confirmed that many were having similar problems. However, the reviewer is right in the fact that there are many ways around this problem. We do describe ours and we are working in a new version of the manuscript with additional data to characterize our new models further and where the method used to create them, although included, is not the main focus of the manuscript. In this new version we will change the title accordingly.

2) Line 104: The authors declare that the efficiency of CRISPR/Cas9 is currently too low to provide therapeutic benefit for DMD in vivo. There are lots of papers that show efficient recovery of dystrophin in small and large animals following CRISPR/Cas9 therapy. The authors should cite them properly.

Thank you for your appreciation. We have reviewed the literature again to include new evidences of efficient dystrophin recovery as well as other studies with lower efficiency.

3) Figures 1, 2,3, and 4 can be merged into one figure.

4) Figure 2A and 2B can be moved to supplementary.

5) Figure 2C and 2D are not clear. Are the duplicates the same? Please invert the black and white colors of the blots.

Thank you for your comments. We have inverted the colors of the blots and changed the marks used in figure 2C and 2D to clarify that duplicates are indeed the same sample, assayed in duplicates. We have also merged figures 1 and 4 and moved figures 2 and 3 to supplementary in this new version.

6) Figure 3: In order to optimize the efficiency of myoblast transfection, the plasmids containing the Cas9 and the sgRNA should have different fluorophores (GFP and mCherry). This approach would increase the percentage of positive edited clones among the clones sorted.

We think the reviewer may have misunderstood our methodology: we are not using a plasmid with the Cas9 and another with the sgRNA, we are using two plasmids, both containing Cas9 and each a different sgRNA. We did try to use two different plasmids, one expressing GFP and one expressing puromycin resistance, but we found out that single GFP positive cell selection plus puromycin selection was too inefficient. We could have tried with two different fluorophores, but we tested the tools we had in our hands first and were successful at obtaining enough clones to continue with their characterization, so we did so instead of a further optimization to our editing protocol.

7) Figure 4A: In the text, the authors state that only 1 clone had the correct genomic edit, but from the PCR genotyping in this figure shows at least 2 positive clones (number 4 and 7).

Thank you for your appreciation. As you said, we got two positive clones (as we also indicate in figure 3B) but we completed the full characterization of one of them (clone number 7= DMD-UTRN-Model). In the new version of the manuscript we explain this further.

8) Figure 4C: The authors should address whether one or both copies of the UTRN gene was edited in their clones.

Thank you for your comment. Both copies of the UTRN gene were edited in our clones. We have included this information both in the text and in the figure 4 legend.

9) Figure 4 B and D: The authors should report the sequence below the electropherograms.

Thank you for this correction, we have included the sequence under the electropherograms.

10) Figure 5B: This western blot is of poor quality. Also, the authors should specify that the samples are differentiated myoblasts. Lastly, a standard protein should be included as a loading control.

Thank you for your comment. Poor quality of dystrophin and utrophin western blots was the main reason to validate a new method in our laboratory to measure these proteins directly in cell culture (1) like an alternative to western blotting. Since then, the myoblot method has been routinely used by us and in collaboration with other groups and companies. We included the western blot as it is sometimes easier for those used to this technique to be able to assess a blot in which there is no dystrophin expression. As you pointed out, our samples were all differentiated myotubes, not myoblasts, and we have modified this accordingly. Thank you very much for pointing out this mistake

On the other hand, as described in the methods, Revert TM 700 Total Protein Stain (Li-Cor) and alpha-actinin were included as standards in dystrophin and utrophin western blots, respectively.

11) Figure 5E: We would like to see triplicates for the level of Utrophin expression.

We thank the reviewer for his/her recommendation, but we do not consider western blotting a good quantitative technique, we have included western blots to show the expression/absence of protein at the same level. We have included many more replicates than needed to show at the level of utrophin by myoblots. We acknowledge that western blotting is the preferred method for some reviewers, so in the new version of our manuscript we clearly indicate the value we give to each technique, being myoblots our choice for quantification.

12) Figure 6: A dystrophin western blot should be included to demonstrate protein recovery following antisense oligonucleotide treatment. Also, the RT-PCR data could be biased as you can have preferential amplification of shorter fragments.

Thank you for your recommendation but as we have explained before, myoblots have been validated in our laboratory to replace western blot for accurate dystrophin quantification in cell culture.

13) Figure 6A: Invert the black and white colors. The authors should also report the control sequences and sequences of the clones under the electropherograms.

Thank you for your suggestion, we have inverted the colors and added the sequences under the electropherograms.

14) Figure 6B: Control myoblasts should be included in figure 5C.

Thank you for this correction, we will include control myoblasts in the new manuscript version.

15) Figure S2A: Invert the black and white colors.

Thank you for your suggestion, we have inverted the colors.

Reviewer #2:

The work from Soblechero-Martín et al reports the generation of a human DMD line deleted for exon 52 using CRISPR technology. In addition, the authors introduced a second mutation that leads to upregulation of utrophin, a protein similar to dystrophin, which has been considered as a therapeutic surrogate. The authors provide a careful description of the methodology used to generate the new cell line and have conducted meticulous evaluations to test the validity of the reagents.

However, if the main purpose of this cell line is to perform drug or small molecule compound screenings, a single line might not be sufficient to draw robust conclusions. The generation of additional DMD lines in different genetic backgrounds using the reagents developed in this study will strengthen the work and will be of interest to the DMD field.

Thank you for your appreciation. We think that a well characterized immortalized culture, like the one we describe is sufficient for compound screening, as described in other recently published studies (2), (3). About the other suggestion, we have indeed used our method to generate other cultures for collaborators, but they will be reported in their own publications, as they are interested in them as tools in their own research projects.

Further, the future use of the edited DMD line with upregulated utrophin is unclear. The utrophin upregulation adds a complexity to this line that might complicate the assessment of screened compounds. In contrast, this line could be used to test if overexpression of utrophin generates myotubes that produce increased force compared to the control DMD line.

We think we may have not explained our screening platform well enough. Our suggestion is to offer our newly generated culture ALONGSIDE the original unedited culture: the original is treated with potential drug candidates, while the new one may or may not be treated, if these drug candidates are thought to act by activating the edited region (see an example in the figure below). In this case, the new culture will be a reliable positive control to the effects that may be reported in the unedited cultures by the drug candidates. We will make this clear in the new version of the manuscript.

Created with BioRender.com

In summary, while there is support and enthusiasm for the techniques and methodological approach of the study, the future use of this single line might be dubious and could be strengthened if additional lines are generated.

We share the reviewer’s enthusiasm for this approach, and we have included in the new version of the manuscript further characterization of this new cell culture that we think would demonstrate its usefulness better.

Author Response:

Evaluation Summary:

Since DBS of the habenula is a new treatment, these are the first data of its kind and potentially of high interest to the field. Although the study mostly confirms findings from animal studies rather than bringing up completely new aspects of emotion processing, it certainly closes a knowledge gap. This paper is of interest to neuroscientists studying emotions and clinicians treating psychiatric disorders. Specifically the paper shows that the habenula is involved in processing of negative emotions and that it is synchronized to the prefrontal cortex in the theta band. These are important insights into the electrophysiology of emotion processing in the human brain.

The authors are very grateful for the reviewers’ positive comments on our study. We also thank all the reviewers for the comments which has helped to improve the manuscript.

Reviewer #1 (Public Review):

The study by Huang et al. report on direct recordings (using DBS electrodes) from the human habenula in conjunction with MEG recordings in 9 patients. Participants were shown emotional pictures. The key finding was a transient increase in theta/alpha activity with negative compared to positive stimuli. Furthermore, there was a later increase in oscillatory coupling in the same band. These are important data, as there are few reports of direct recordings from the habenula together with the MEG in humans performing cognitive tasks. The findings do provide novel insight into the network dynamics associated with the processing of emotional stimuli and particular the role of the habenula.

Recommendations:

How can we be sure that the recordings from the habenula are not contaminated by volume conduction; i.e. signals from neighbouring regions? I do understand that bipolar signals were considered for the DBS electrode leads. However, high-frequency power (gamma band and up) is often associated with spiking/MUA and considered less prone to volume conduction. I propose to also investigate that high-frequency gamma band activity recorded from the bipolar DBS electrodes and relate to the emotional faces. This will provide more certainty that the measured activity indeed stems from the habenula.

We thank the reviewer for the comment. As the reviewer pointed out, bipolar macroelectrode can detect locally generated potentials, as demonstrated in the case of recordings from subthalamic nucleus and especially when the macroelectrodes are inside the subthalamic nucleus (Marmor et al., 2017). However, considering the size of the habenula and the size of the DBS electrode contacts, we have to acknowledge that we cannot completely exclude the possibility that the recordings are contaminated by volume conduction of activities from neighbouring areas, as shown in Bertone-Cueto et al. 2019. We have now added extra information about the size of the habenula and acknowledged the potential contamination of activities from neighbouring areas through volume conduction in the ‘Limitation’:

"Another caveat we would like to acknowledge that the human habenula is a small region. Existing data from structural MRI scans reported combined habenula (the sum of the left and right hemispheres) volumes of ~ 30–36 mm3 (Savitz et al., 2011a; Savitz et al., 2011b) which means each habenula has the size of 2~3 mm in each dimension, which may be even smaller than the standard functional MRI voxel size (Lawson et al., 2013). The size of the habenula is also small relative to the standard DBS electrodes (as shown in Fig. 2A). The electrodes used in this study (Medtronic 3389) have electrode diameter of 1.27 mm with each contact length of 1.5 mm, and contact spacing of 0.5 mm. We have tried different ways to confirm the location of the electrode and to select the contacts that is within or closest to the habenula: 1.) the MRI was co-registered with a CT image (General Electric, Waukesha, WI, USA) with the Leksell stereotactic frame to obtain the coordinate values of the tip of the electrode; 2.) Post-operative CT was co-registered to pre-operative T1 MRI using a two-stage linear registration using Lead-DBS software. We used bipolar signals constructed from neighbouring macroelectrode recordings, which have been shown to detect locally generated potentials from subthalamic nucleus and especially when the macroelectrodes are inside the subthalamic nucleus (Marmor et al., 2017). Considering that not all contacts for bipolar LFP construction are in the habenula in this study, as shown in Fig. 2, we cannot exclude the possibility that the activities we measured are contaminated by activities from neighbouring areas through volume conduction. In particular, the human habenula is surrounded by thalamus and adjacent to the posterior end of the medial dorsal thalamus, so we may have captured activities from the medial dorsal thalamus. However, we also showed that those bipolar LFPs from contacts in the habenula tend to have a peak in the theta/alpha band in the power spectra density (PSD); whereas recordings from contacts outside the habenula tend to have extra peak in beta frequency band in the PSD. This supports the habenula origin of the emotional valence related changes in the theta/alpha activities reported here."

We have also looked at gamma band oscillations or high frequency activities in the recordings. However, we didn’t observe any peak in high frequency band in the average power spectral density, or any consistent difference in the high frequency activities induced by the emotional stimuli (Fig. S1). We suspect that high frequency activities related to MUA/spiking are very local and have very small amplitude, so they are not picked up by the bipolar LFPs measured from contacts with both the contact area for each contact and the between-contact space quite large comparative to the size of the habenula.

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Figure S1. (A) Power spectral density of habenula LFPs across all time period when emotional stimuli were presented. The bold blue line and shadowed region indicates the mean ± SEM across all recorded hemispheres and the thin grey lines show measurements from individual hemispheres. (B) Time-frequency representations of the power response relative to pre-stimulus baseline for different conditions showing habenula gamma and high frequency activity are not modulated by emotional

References:

Savitz JB, Bonne O, Nugent AC, Vythilingam M, Bogers W, Charney DS, et al. Habenula volume in post-traumatic stress disorder measured with high-resolution MRI. Biology of Mood & Anxiety Disorders 2011a; 1(1): 7.

Savitz JB, Nugent AC, Bogers W, Roiser JP, Bain EE, Neumeister A, et al. Habenula volume in bipolar disorder and major depressive disorder: a high-resolution magnetic resonance imaging study. Biological Psychiatry 2011b; 69(4): 336-43.

Lawson RP, Drevets WC, Roiser JP. Defining the habenula in human neuroimaging studies. NeuroImage 2013; 64: 722-7.

Marmor O, Valsky D, Joshua M, Bick AS, Arkadir D, Tamir I, et al. Local vs. volume conductance activity of field potentials in the human subthalamic nucleus. Journal of Neurophysiology 2017; 117(6): 2140-51.

Bertone-Cueto NI, Makarova J, Mosqueira A, García-Violini D, Sánchez-Peña R, Herreras O, et al. Volume-Conducted Origin of the Field Potential at the Lateral Habenula. Frontiers in Systems Neuroscience 2019; 13:78.

Figure 3: the alpha/theta band activity is very transient and not band-limited. Why refer to this as oscillatory? Can you exclude that the TFRs of power reflect the spectral power of ERPs rather than modulations of oscillations? I propose to also calculate the ERPs and perform the TFR of power on those. This might result in a re-interpretation of the early effects in theta/alpha band.

We agree with the reviewer that the activity increase in the first time window with short latency after the stimuli onset is very transient and not band-limited. This raise the question that whether this is oscillatory or a transient evoked activity. We have now looked at this initial transient activity in different ways: 1.) We quantified the ERP in LFPs locked to the stimuli onset for each emotional valence condition and for each habenula. We investigated whether there was difference in the amplitude or latency of the ERP for different stimuli emotional valence conditions. As showing in the following figure, there is ERP with stimuli onset with a positive peak at 402 ± 27 ms (neutral stimuli), 407 ± 35 ms (positive stimuli), 399 ± 30 ms (negative stimuli). The flowing figure (Fig. 3–figure supplement 1) will be submitted as figure supplement related to Fig. 3. However, there was no significant difference in ERP latency or amplitude caused by different emotional valence stimuli. 2.) We have quantified the pure non-phase-locked (induced only) power spectra by calculating the time-frequency power spectrogram after subtracting the ERP (the time-domain trial average) from time-domain neural signal on each trial (Kalcher and Pfurtscheller, 1995; Cohen and Donner, 2013). This shows very similar results as we reported in the main manuscript, as shown in Fig. 3–figure supplement 2. These further analyses show that even though there were event related potential changes time locked around the stimuli onset, and this ERP did NOT contribute to the initial broad-band activity increase at the early time window shown in plot A-C in Figure 3. The figures of the new analyses and following have now been added in the main text:

"In addition, we tested whether stimuli-related habenula LFP modulations primarily reflect a modulation of oscillations, which is not phase-locked to stimulus onset, or, alternatively, if they are attributed to evoked event-related potential (ERP). We quantified the ERP for each emotional valence condition for each habenula. There was no significant difference in ERP latency or amplitude caused by different emotional valence stimuli (Fig. 3–figure supplement 1). In addition, when only considering the non phase-locked activity by removing the ERP from the time series before frequency-time decomposition, the emotional valence effect (presented in Fig. 3–figure supplement 2) is very similar to those shown in Fig.3. These additional analyses demonstrated that the emotional valence effect in the LFP signal is more likely to be driven by non-phase-locked (induced only) activity."

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Fig. 3–figure supplement 1. Event-related potential (ERP) in habenula LFP signals in different emotional valence (neutral, positive and negative) conditions. (A) Averaged ERP waveforms across patients for different conditions. (B) Peak latency and amplitude (Mean ± SEM) of the ERP components for different conditions.

Fig. 3–figure supplement 2. Non-phase-locked activity in different emotional valence (neutral, positive and negative) conditions (N = 18). (A) Time-frequency representation of the power changes relative to pre-stimulus baseline for three conditions. Significant clusters (p < 0.05, non-parametric permutation test) are encircled with a solid black line. (B) Time-frequency representation of the power response difference between negative and positive valence stimuli, showing significant increased activity the theta/alpha band (5-10 Hz) at short latency (100-500 ms) and another increased theta activity (4-7 Hz) at long latencies (2700-3300 ms) with negative stimuli (p < 0.05, non-parametric permutation test). (C) Normalized power of the activities at theta/alpha (5-10 Hz) and theta (4-7 Hz) band over time. Significant difference between the negative and positive valence stimuli is marked by a shadowed bar (p < 0.05, corrected for multiple comparison).

References:

Kalcher J, Pfurtscheller G. Discrimination between phase-locked and non-phase-locked event-related EEG activity. Electroencephalography and Clinical Neurophysiology 1995; 94(5): 381-4.

Cohen MX, Donner TH. Midfrontal conflict-related theta-band power reflects neural oscillations that predict behavior. Journal of Neurophysiology 2013; 110(12): 2752-63.

Figure 4D: can you exclude that the frontal activity is not due to saccade artifacts? Only eye blink artifacts were reduced by the ICA approach. Trials with saccades should be identified in the MEG traces and rejected prior to further analysis.

We understand and appreciate the reviewer’s concern on the source of the activity modulations shown in Fig. 4D. We tried to minimise the eye movement or saccade in the recording by presenting all figures at the centre of the screen, scaling all presented figures to similar size, and presenting a white cross at the centre of the screen preparing the participants for the onset of the stimuli. Despite this, participants my still make eye movements and saccade in the recording. We used ICA to exclude the low frequency large amplitude artefacts which can be related to either eye blink or other large eye movements. However, this may not be able to exclude artefacts related to miniature saccades. As shown in Fig. 4D, on the sensor level, the sensors with significant difference between the negative vs. positive emotional valence condition clustered around frontal cortex, close to the eye area. However, we think this is not dominated by saccades because of the following two reasons:

1.) The power spectrum of the saccadic spike artifact in MEG is characterized by a broadband peak in the gamma band from roughly 30 to 120 Hz (Yuval-Greenberg et al., 2008; Keren et al., 2010). In this study the activity modulation we observed in the frontal sensors are limited to the theta/alpha frequency band, so it is different from the power spectra of the saccadic spike artefact.

2.) The source of the saccadic spike artefacts in MEG measurement tend to be localized to the region of the extraocular muscles of both eyes (Carl et al., 2012).We used beamforming source localisation to identify the source of the activity modulation reported in Fig. 4D. This beamforming analysis identified the source to be in the Broadmann area 9 and 10 (shown in Fig. 5). This excludes the possibility that the activity modulation in the sensor level reported in Fig. 4D is due to saccades. In addition, Broadman area 9 and 10, have previously been associated with emotional stimulus processing (Bermpohl et al., 2006), Broadman area 9 in the left hemisphere has also been used as the target for repetitive transcranial magnetic stimulation (rTMS) as a treatment for drug-resistant depression (Cash et al., 2020). The source localisation results, together with previous literature on the function of the identified source area suggest that the activity modulation we observed in the frontal cortex is very likely to be related to emotional stimuli processing.

References:

Yuval-Greenberg S, Tomer O, Keren AS, Nelken I, Deouell LY. Transient induced gamma-band response in EEG as a manifestation of miniature saccades. Neuron 2008; 58(3): 429-41.

Keren AS, Yuval-Greenberg S, Deouell LY. Saccadic spike potentials in gamma-band EEG: characterization, detection and suppression. NeuroImage 2010; 49(3): 2248-63.

Carl C, Acik A, Konig P, Engel AK, Hipp JF. The saccadic spike artifact in MEG. NeuroImage 2012; 59(2): 1657-67.

Bermpohl F, Pascual-Leone A, Amedi A, Merabet LB, Fregni F, Gaab N, et al. Attentional modulation of emotional stimulus processing: an fMRI study using emotional expectancy. Human Brain Mapping 2006; 27(8): 662-77.

Cash RFH, Weigand A, Zalesky A, Siddiqi SH, Downar J, Fitzgerald PB, et al. Using Brain Imaging to Improve Spatial Targeting of Transcranial Magnetic Stimulation for Depression. Biological Psychiatry 2020.

The coherence modulations in Fig 5 occur quite late in time compared to the power modulations in Fig 3 and 4. When discussing the results (in e.g. the abstract) it reads as if these findings are reflecting the same process. How can the two effect reflect the same process if the timing is so different?

As the reviewer pointed out correctly, the time window where we observed the coherence modulations happened quite late in time compared to the initial power modulations in the frontal cortex and the habenula (Fig. 4). And there was another increase in the theta band activities in the habenula area even later, at around 3 second after stimuli onset when the emotional figure has already disappeared. Emotional response is composed of a number of factors, two of which are the initial reactivity to an emotional stimulus and the subsequent recovery once the stimulus terminates or ceases to be relevant (Schuyler et al., 2014). We think these neural effects we observed in the three different time windows may reflect different underlying processes. We have discussed this in the ‘Discussion’:

"These activity changes at different time windows may reflect the different neuropsychological processes underlying emotion perception including identification and appraisal of emotional material, production of affective states, and autonomic response regulation and recovery (Phillips et al., 2003a). The later effects of increased theta activities in the habenula when the stimuli disappeared were also supported by other literature showing that, there can be prolonged effects of negative stimuli in the neural structure involved in emotional processing (Haas et al., 2008; Puccetti et al., 2021). In particular, greater sustained patterns of brain activity in the medial prefrontal cortex when responding to blocks of negative facial expressions was associated with higher scores of neuroticism across participants (Haas et al., 2008). Slower amygdala recovery from negative images also predicts greater trait neuroticism, lower levels of likability of a set of social stimuli (neutral faces), and declined day-to-day psychological wellbeing (Schuyler et al., 2014; Puccetti et al., 2021)."

References:

Schuyler BS, Kral TR, Jacquart J, Burghy CA, Weng HY, Perlman DM, et al. Temporal dynamics of emotional responding: amygdala recovery predicts emotional traits. Social Cognitive and Affective Neuroscience 2014; 9(2): 176-81.

Phillips ML, Drevets WC, Rauch SL, Lane R. Neurobiology of emotion perception I: The neural basis of normal emotion perception. Biological Psychiatry 2003a; 54(5): 504-14.

Haas BW, Constable RT, Canli T. Stop the sadness: Neuroticism is associated with sustained medial prefrontal cortex response to emotional facial expressions. NeuroImage 2008; 42(1): 385-92.

Puccetti NA, Schaefer SM, van Reekum CM, Ong AD, Almeida DM, Ryff CD, et al. Linking Amygdala Persistence to Real-World Emotional Experience and Psychological Well-Being. Journal of Neuroscience 2021: JN-RM-1637-20.

Be explicit on the degrees of freedom in the statistical tests given that one subject was excluded from some of the tests.

We thank the reviewers for the comment. The number of samples used for each statistics analysis are stated in the title of the figures. We have now also added the degree of freedom in the main text when parametric statistical tests such as t-test or ANOVAs have been used. When permutation tests (which do not have any degrees of freedom associated with it) are used, we have now added the number of samples for the permutation test.

Reviewer #2 (Public Review):

In this study, Huang and colleagues recorded local field potentials from the lateral habenula in patients with psychiatric disorders who recently underwent surgery for deep brain stimulation (DBS). The authors combined these invasive measurements with non-invasive whole-head MEG recordings to study functional connectivity between the habenula and cortical areas. Since the lateral habenula is believed to be involved in the processing of emotions, and negative emotions in particular, the authors investigated whether brain activity in this region is related to emotional valence. They presented pictures inducing negative and positive emotions to the patients and found that theta and alpha activity in the habenula and frontal cortex increases when patients experience negative emotions. Functional connectivity between the habenula and the cortex was likewise increased in this band. The authors conclude that theta/alpha oscillations in the habenula-cortex network are involved in the processing of negative emotions in humans.

Because DBS of the habenula is a new treatment tested in this cohort in the framework of a clinical trial, these are the first data of its kind. Accordingly, they are of high interest to the field. Although the study mostly confirms findings from animal studies rather than bringing up completely new aspects of emotion processing, it certainly closes a knowledge gap.

In terms of community impact, I see the strengths of this paper in basic science rather than the clinical field. The authors demonstrate the involvement of theta oscillations in the habenula-prefrontal cortex network in emotion processing in the human brain. The potential of theta oscillations to serve as a marker in closed-loop DBS, as put forward by the authors, appears less relevant to me at this stage, given that the clinical effects and side-effects of habenula DBS are not known yet.

We thank the reviewers for the favourable comments about the implication of our study in basic science and about the value of our study in closing a knowledge gap. We agree that further studies would be required to make conclusions about the clinical effects and side-effects of habenula DBS.

Detailed comments:

The group-average MEG power spectrum (Fig. 4B) suggests that negative emotions lead to a sustained theta power increase and a similar effect, though possibly masked by a visual ERP, can be seen in the habenula (Fig. 3C). Yet the statistics identify brief elevations of habenula theta power at around 3s (which is very late), a brief elevation of prefrontal power a time 0 or even before (Fig. 4C) and a brief elevation of Habenula-MEG theta coherence around 1 s. It seems possible that this lack of consistency arises from a low signal-to-noise ratio. The data contain only 27 trails per condition on average and are contaminated by artifacts caused by the extension wires.

With regard to the nature of the activity modulation with short latency after stimuli onset: whether this is an ERP or oscillation? We have now investigated this. In summary, by analysing the ERP and removing the influence of the ERP from the total power spectra, we didn’t observe stimulus emotional valence related modulation in the ERP, and the modulation related to emotional valence in the pure induced (non-phase-locked) power spectra was similar to what we have observed in the total power shown in Fig. 3. Therefore, we argue that the theta/alpha increase with negative emotional stimuli we observed in both habenula and prefrontal cortex 0-500 ms after stimuli onset are not dominated by visual or other ERP.

With regard to the signal-to-noise ratio from only 27 trials per condition on average per participant: We have tried to clean the data by removing the trials with obvious artefacts characterised by increased measurements in the time domain over 5 times the standard deviation and increased activities across all frequency bands in the frequency domain. After removing the trials with artefacts, we have 27 trials per condition per subject on average. We agree that 27 trials per condition on average is not a high number, and increasing the number of trials would further increase the signal-to-noise ratio. However, our studies with EEG recordings and LFP recordings from externalised patients have shown that 30 trials was enough to identify reduction in the amplitude of post-movement beta oscillations at the beginning of visuomotor adaption in the motor cortex and STN (Tan et al., 2014a; Tan et al., 2014b). These results of motor error related modulation in the post-movement beta have been repeated by other studies from other groups. In Tan et al. 2014b, with simultaneous EEG and STN LFP measurements and a similar number of trials (around 30), we also quantified the time-course of STN-motor cortex coherence during voluntary movements. This pattern has also been repeated in a separate study from another group with around 50 trials per participant (Talakoub et al., 2016). In addition, similar behavioural paradigm (passive figure viewing paradigm) has been used in two previous studies with LFP recordings from STN from different patient groups (Brucke et al., 2007; Huebl et al., 2014). In both studies, a similar number of trials per condition around 27 was used. The authors have identified meaningful activity modulation in the STN by emotional stimuli. Therefore, we think the number of trials per condition was sufficient to identify emotional valence induced difference in the LFPs in the paradigm.

We agree that the measurement of coherence can be more susceptible to noise and suffer from the reduced signal-to-noise ratio in MEG recording. In Hirschmann et al. 2013, 5 minutes of resting recording and 5 minutes of movement recording from 10 PD patients were used to quantify movement related changes in STN-cortical coherence and how this was modulated by levodopa (Hirschmann et al., 2013). Litvak et al. (2012) have identified movement-related changes in the coherence between STN LFP and motor cortex with recording with simultaneous STN LFP and MEG recordings from 17 PD patients and 20 trials in average per participant per condition (Litvak et al., 2012). With similar methods, van Wijk et al. (2017) used recordings from 9 patients and around on average in 29 trials per hand per condition, and they identified reduced cortico-pallidal coherence in the low-beta decreases during movement (van Wijk et al., 2017). So the trial number per condition participant we used in this study are comparable to previous studies.

The DBS extension wires do reduce signal-to-noise ratio in the MEG recording. therefore the spatiotemporal Signal Space Separation (tSSS) method (Taulu and Simola, 2006) implemented in the MaxFilter software (Elekta Oy, Helsinki, Finland) has been applied in this study to suppress strong magnetic artifacts caused by extension wires. This method has been proved to work well in de-noising the magnetic artifacts and movement artifacts in MEG data in our previous studies (Cao et al., 2019; Cao et al., 2020). In addition, the beamforming method proposed by several studies (Litvak et al., 2010; Hirschmann et al., 2011; Litvak et al., 2011) has been used in this study. In Litvak et al., 2010, the artifacts caused by DBS extension wires was detailed described and the beamforming was demonstrated to effectively suppress artifacts and thereby enable both localization of cortical sources coherent with the deep brain nucleus. We have now added more details and these references about the data cleaning and the beamforming method in the main text. With the beamforming method, we did observe the standard movement-related modulation in the beta frequency band in the motor cortex with 9 trials of figure pressing movements, shown in the following figure for one patient as an example (Figure 5–figure supplement 1). This suggests that the beamforming method did work well to suppress the artefacts and help to localise the source with a low number of trials. The figure on movement-related modulation in the motor cortex in the MEG signals have now been added as a supplementary figure to demonstrate the effect of the beamforming.

Figure 5–figure supplement 1. (A) Time-frequency maps of MEG activity for right hand button press at sensor level from one participant (Case 8). (B) DICS beamforming source reconstruction of the areas with movement-related oscillation changes in the range of 12-30 Hz. The peak power was located in the left M1 area, MNI coordinate [-37, -12, 43].

References:

Tan H, Jenkinson N, Brown P. Dynamic neural correlates of motor error monitoring and adaptation during trial-to-trial learning. Journal of Neuroscience 2014a; 34(16): 5678-88.

Tan H, Zavala B, Pogosyan A, Ashkan K, Zrinzo L, Foltynie T, et al. Human subthalamic nucleus in movement error detection and its evaluation during visuomotor adaptation. Journal of Neuroscience 2014b; 34(50): 16744-54.

Talakoub O, Neagu B, Udupa K, Tsang E, Chen R, Popovic MR, et al. Time-course of coherence in the human basal ganglia during voluntary movements. Scientific Reports 2016; 6: 34930.

Brucke C, Kupsch A, Schneider GH, Hariz MI, Nuttin B, Kopp U, et al. The subthalamic region is activated during valence-related emotional processing in patients with Parkinson's disease. European Journal of Neuroscience 2007; 26(3): 767-74.

Huebl J, Spitzer B, Brucke C, Schonecker T, Kupsch A, Alesch F, et al. Oscillatory subthalamic nucleus activity is modulated by dopamine during emotional processing in Parkinson's disease. Cortex 2014; 60: 69-81.

Hirschmann J, Ozkurt TE, Butz M, Homburger M, Elben S, Hartmann CJ, et al. Differential modulation of STN-cortical and cortico-muscular coherence by movement and levodopa in Parkinson's disease. NeuroImage 2013; 68: 203-13.

Litvak V, Eusebio A, Jha A, Oostenveld R, Barnes G, Foltynie T, et al. Movement-related changes in local and long-range synchronization in Parkinson's disease revealed by simultaneous magnetoencephalography and intracranial recordings. Journal of Neuroscience 2012; 32(31): 10541-53.

van Wijk BCM, Neumann WJ, Schneider GH, Sander TH, Litvak V, Kuhn AA. Low-beta cortico-pallidal coherence decreases during movement and correlates with overall reaction time. NeuroImage 2017; 159: 1-8.

Taulu S, Simola J. Spatiotemporal signal space separation method for rejecting nearby interference in MEG measurements. Physics in Medicine and Biology 2006; 51(7): 1759-68.

Cao C, Huang P, Wang T, Zhan S, Liu W, Pan Y, et al. Cortico-subthalamic Coherence in a Patient With Dystonia Induced by Chorea-Acanthocytosis: A Case Report. Frontiers in Human Neuroscience 2019; 13: 163.

Cao C, Li D, Zhan S, Zhang C, Sun B, Litvak V. L-dopa treatment increases oscillatory power in the motor cortex of Parkinson's disease patients. NeuroImage Clinical 2020; 26: 102255.

Litvak V, Eusebio A, Jha A, Oostenveld R, Barnes GR, Penny WD, et al. Optimized beamforming for simultaneous MEG and intracranial local field potential recordings in deep brain stimulation patients. NeuroImage 2010; 50(4): 1578-88.

Litvak V, Jha A, Eusebio A, Oostenveld R, Foltynie T, Limousin P, et al. Resting oscillatory cortico-subthalamic connectivity in patients with Parkinson's disease. Brain 2011; 134(Pt 2): 359-74.

Hirschmann J, Ozkurt TE, Butz M, Homburger M, Elben S, Hartmann CJ, et al. Distinct oscillatory STN-cortical loops revealed by simultaneous MEG and local field potential recordings in patients with Parkinson's disease. NeuroImage 2011; 55(3): 1159-68.

I doubt that the correlation between habenula power and habenula-MEG coherence (Fig. 6C) is informative of emotion processing. First, power and coherence in close-by time windows are likely to to be correlated irrespective of the task/stimuli. Second, if meaningful, one would expect the strongest correlation for the negative condition, as this is the only condition with an increase of theta coherence and a subsequent increase of theta power in the habenula. This, however, does not appear to be the case.

The authors included the factors valence and arousal in their linear model and found that only valence correlated with electrophysiological effects. I suspect that arousal and valence scores are highly correlated. When fed with informative yet highly correlated variables, the significance of individual input variables becomes difficult to assess in many statistical models. Hence, I am not convinced that valence matters but arousal not.

For the correlation shown in Fig. 6C, we used a linear mixed-effect modelling (‘fitlme’ in Matlab) with different recorded subjects as random effects to investigate the correlations between the habenula power and habenula-MEG coherence at an earlier window, while considering all trials together. Therefore the reported value in the main text and in the figure (k = 0.2434 ± 0.1031, p = 0.0226, R2 = 0.104) show the within subjects correlation that are consistent across all measured subjects. The correlation is likely to be mediated by emotional valence condition, as negative emotional stimuli tend to be associated with both high habenula-MEG coherence and high theta power in the later time window tend to happen in the trials with.

The arousal scores are significantly different for the three valence conditions as shown in Fig. 1B. However, the arousal scores and the valence scores are not monotonically correlated, as shown in the following figure (Fig. S2). The emotional neutral figures have the lowest arousal value, but have the valence value sitting between the negative figures and the positive figures. We have now added the following sentence in the main text:

"This nonlinear and non-monotonic relationship between arousal scores and the emotional valence scores allowed us to differentiate the effect of the valence from arousal."

Table 2 in the main text show the results of the linear mixed-effect modelling with the neural signal as the dependent variable and the valence and arousal scores as independent variables. Because of the non-linear and non-monotonic relationship between the valence and arousal scores, we think the significance of individual input variables is valid in this statistical model. We have now added a new figure (shown below, Fig. 7) with scatter plots showing the relationship between the electrophysiological signal and the arousal and emotional valence scores separately using Spearman’s partial correlation analysis. In each scatter plot, each dot indicates the average measurement from one participant in one emotional valence condition. As shown in the following figure, the electrophysiological measurements linearly correlated with the valence score, but not with the arousal scores. However, the statistics reported in this figure considered all the dots together. The linear mixed effect modelling taking into account the interdependency of the measurements from the same participant. So the results reported in the main text using linear mixed effect modelling are statistically more valid, but supplementary figure here below illustrate the relationship.

Figure S2. Averaged valence and arousal ratings (mean ± SD) for figures of the three emotional condition. (B) Scatter plots showing the relationship between arousal and valence scores for each emotional condition for each participant.

Figure 7. Scatter plots showing how early theta/alpha band power increase in the frontal cortex (A), theta/alpha band frontal cortex-habenula coherence (B) and theta band power increase in habenula stimuli (C) changed with emotional valence (left column) and arousal (right column). Each dot shows the average of one participant in each categorical valence condition, which are also the source data of the multilevel modelling results presented in Table 2. The R and p value in the figure are the results of partial correlation considering all data points together.

Page 8: "The time-varying coherence was calculated for each trial". This is confusing because coherence quantifies the stability of a phase difference over time, i.e. it is a temporal average, not defined for individual trials. It has also been used to describe the phase difference stability over trials rather than time, and I assume this is the method applied here. Typically, the greatest coherence values coincide with event-related power increases, which is why I am surprised to see maximum coherence at 1s rather than immediately post-stimulus.

We thank the reviewer for pointing out this incorrect description. As the reviewer pointed out correctly, the method we used describe the phase difference stability over trials rather than time. We have now clarified how coherence was calculated and added more details in the methods:

"The time-varying cross trial coherence between each MEG sensor and the habenula LFP was first calculated for each emotional valence condition. For this, time-frequency auto- and cross-spectral densities in the theta/alpha frequency band (5-10 Hz) between the habenula LFP and each MEG channel at sensor level were calculated using the wavelet transform-based approach from -2000 to 4000 ms for each trial with 1 Hz steps using the Morlet wavelet and cycle number of 6. Cross-trial coherence spectra for each LFP-MEG channel combination was calculated for each emotional valence condition for each habenula using the function ‘ft_connectivityanalysis’ in Fieldtrip (version 20170628). Stimulus-related changes in coherence were assessed by expressing the time-resolved coherence spectra as a percentage change compared to the average value in the -2000 to -200 ms (pre-stimulus) time window for each frequency."

In the Morlet wavelet analysis we used here, the cycle number (C) determines the temporal resolution and frequency resolution for each frequency (F). The spectral bandwidth at a given frequency F is equal to 2F/C while the wavelet duration is equal to C/F/pi. We used a cycle number of 6. For theta band activities around 5 Hz, we will have the spectral bandwidth of 25/6 = 1.7 Hz and the wavelet duration of 6/5/pi = 0.38s = 380ms.

As the reviewer noticed, we observed increased activities across a wide frequency band in both habenula and the prefrontal cortex within 500 ms after stimuli onset. But the increase of cross-trial coherence starts at around 300 ms. The increase of coherence in a time window without increase of power in either of the two structures indicates a phase difference stability across trials in the oscillatory activities from the two regions, and this phase difference stability across trials was not secondary to power increase.

Reviewer #3 (Public Review):

This paper describes the oscillatory activity of the habenula using local field potentials, both within the region and, through the use of MEG, in connection to the prefrontal cortex. The characteristics of this activity were found to vary with the emotional valence but not with arousal. Sheding light on this is relevant, because the habenula is a promising target for deep brain stimulation.

In general, because I am not much on top of the literature on the habenula, I find difficult to judge about the novelty and the impact of this study. What I can say is that I do find the paper is well-written and very clear; and the methods, although quite basic (which is not bad), are sound and rigourous.

We thank the reviewer for the positive comments about the potential implication of our study and on the methods we used.

On the less positive side, even though I am aware that in this type of studies it is difficult to have high N, the very low N in this case makes me worry about the robustness and replicability of the results. I'm sure I have missed it and it's specified somewhere, but why is N different for the different figures? Is it because only 8 people had MEG? The number of trials seems also a somewhat low. Therefore, I feel the authors perhaps need to make an effort to make up for the short number of subjects in order to add confidence to the results. I would strongly recommend to bootstrap the statistical analysis and extract non-parametric confidence intervals instead of showing parametric standard errors whenever is appropriate. When doing that, it must be taken into account that each two of the habenula belong to the same person; i.e. one bootstraps the subjects not the habenula.

We do understand and appreciate the concern of the reviewer on the low sample numbers due to the strict recruitment criteria for this very early stage clinical trial: 9 patients for bilateral habenula LFPs, and 8 patients with good quality MEGs. Some information to justify the number of trials per condition for each participant has been provided in the reply to the Detailed Comments 1 from Reviewer 2. The sample number used in each analysis was included in the figures and in the main text.

We have used non-parametric cluster-based permutation approach (Maris and Oostenveld, 2007) for all the main results as shown in Fig. 3-5. Once the clusters (time window and frequency band) with significant differences for different emotional valence conditions have been identified, parametric statistical test was applied to the average values of the clusters to show the direction of the difference. These parametric statistics are secondary to the main non-parametric permutation test.

In addition, the DICS beamforming method was applied to localize cortical sources exhibiting stimuli-related power changes and cortical sources coherent with deep brain LFPs for each subject for positive and negative emotional valence conditions respectively. After source analysis, source statistics over subjects was performed. Non-parametric permutation testing with or without cluster-based correction for multiple comparisons was applied to statistically quantify the differences in cortical power source or coherence source between negative and positive emotional stimuli.

References:

Maris E, Oostenveld R. Nonparametric statistical testing of EEG- and MEG-data. Journal of Neuroscience Methods 2007; 164(1): 177-90.

Related to this point, the results in Figure 6 seem quite noisy, because interactions (i.e. coherence) are harder to estimate and N is low. For example, I have to make an effort of optimism to believe that Fig 6A is not just noise, and the result in Fig 6C is also a bit weak and perhaps driven by the blue point at the bottom. My read is that the authors didn't do permutation testing here, and just a parametric linear-mixed effect testing. I believe the authors should embed this into permutation testing to make sure that the extremes are not driving the current p-value.

We have now quantified the coherence between frontal cortex-habenula and occipital cortex-habenula separately (please see more details in the reply to Reviewer 2 (Recommendations for the authors 6). The new analysis showed that the increase in the theta/alpha band coherence around 1 s after the negative stimuli was only observed between prefrontal cortex-habenula and not between occipital cortex-habenula. This supports the argument that Fig. 6A is not just noise.

Author Response

Reviewer #1:

Köster and colleagues present a brief report in which they study in 9 month-old babies the electrophysiological responses to expected and unexpected events. The major finding is that in addition to a known ERP response, an NC present between 400-600 ms, they observe a differential effect in theta oscillations. The latter is a novel result and it is linked to the known properties of theta oscillations in learning. This is a nice study, with novel results and well presented. My major reservation however concerns the push the authors make for the novelty of the results and their interpretation as reflecting brain dynamics and rhythms. The reason for that is, that any ERP, passed through the lens of a wavelet/FFT etc, will yield a response at a particular frequency. This is especially the case for families of ERP responses related to unexpected event e.g., MMR, and NC, etc. For which there is plenty of literature linking them to responses to surprising event, and in particular in babies; and which given their timing will be reflected in delta/theta oscillations. The reason why I am pressing on this issue, is because there is an old, but still ongoing debate attempting to dissociate intrinsic brain dynamics from simple event related responses. This is by no means trivial and I certainly do not expect the authors to resolve it, yet I would expect the authors to be careful in their interpretation, to warn the reader that the result could just reflect the known ERP, to avoid introducing confusion in the field.

We would like to thank the author for highlighting the novelty of the results. Critically, there is one fundamental difference in investigating the ERP response and the trial-wise oscillatory power, which we have done in the present analysis: when looking at the evoked oscillatory response (i.e., the TF characteristics of the ERP), the signal is averaged over trials first and then subjected to a wavelet transform. However, when looking at the ongoing (or total) oscillatory response, the wavelet transform is applied at the level of the single trial, before the TF response of the single trials is averaged across the trials of one condition trials (for a classical illustration, see Tallon-Baudry & Bertrand, 1999; TICS, Box 2). We have now made this distinction more salient throughout the manuscript.

In the present study, the results did not suggest a relation between the ERP and the ongoing theta activity, because the topography, temporal evolution, and polarity of the ERP and the theta response were very dissimilar: Looking at Figure 2 (A and B) and Figure 3 (B and C), the Nc peaks at central electrodes, but the theta response is more distributed, and the expected versus unexpected difference was specific for the .4 to .6 s time window, but the theta difference lasted the whole trial. Furthermore, the NC was higher for expected versus unexpected, which should (due to the low frequency) rather lead to a higher theta power for unexpected, in contrast to expected events for the time frequency analysis for the Nc. To verify this intuition, we now ran a wavelet analysis on the evoked response (i.e., the ERP) and, for a direct comparison, also plotted the ongoing oscillatory response for the central electrodes (see Additional Figure 1). These additional analyses nicely illustrate that the trial-wise theta response provides a fundamentally different approach to analyze oscillatory brain dynamics.

Because this is likely of interest to many readers, we also report the results of the wavelet analysis of the ERP versus the analysis of the ongoing theta activity at central electrodes and the corresponding statistics in the result section, and have also included the Additional Figure in the supplementary materials, as Figure S2.

Additional Figure 1. Comparison of the topography and time course for the 4 – 5 Hz activity for the evoked (A, B) and the ongoing (C, D) oscillatory response at central electrodes (400 – 600 ms; Cz, C3, C4; baseline: -100 – 0 ms). (A) Topography for the difference between unexpected and expected events in the evoked oscillatory response. (B) The corresponding time course at central electrodes, which did not reveal a significant difference between 400 – 600 ms, t(35) = 1.57, p = .126. (C) Topography for the same contrast in the ongoing oscillatory response and (D) the corresponding time course at central electrodes, which did likewise not reveal a significant difference between 400 – 600 ms, t(35) = -1.26, p = .218. The condition effects (unexpected - expected) were not correlated between the evoked and the ongoing response, r = .23, p = .169.

A second aspect that I would like the authors to comment on is the power of the experimental design to measure surprise. From the methods, I gathered that the same stimulus materials and with the same frequency were presented as expected and unexpected endings. If that is the case, what is the measure of surprise? For once the same materials are shown causing habituation and reducing novelty and second the experiment introduces a long-term expectation of a 50:50 proportion of expected/unexpected events. I might be missing something here, which is likely as the methods are quite sparse in the description of what was actually done.

We have used 4 different stimuli types (variants) in each of the 4 different domains, with either an expected or unexpected outcome. This resulted in 32 distinct stimulus sequences, which we presented twice, resulting in (up to) 64 trials. We have now described this approach and design in more detail and have also included all stimuli as supplementary material (Figure S1). In particular, we have used multiple types in each domain to reduce potential habituation or expectation effects. Still, we agree that one difficulty may be that, over time, infants got used to the fact that expected and unexpected outcomes were to be similarly “expected” (i.e., 50:50). However, if this was the case it would have resulted in a reduction (or disappearance) of the condition effect, and would thus also reduce the condition difference that we found, rather than providing an alternative explanation. We now included this consideration in the method section (p. 7).

Two more comments concerning the analysis choices:

1) The statistics for the ERP and the TF could be reported using a cluster size correction. These are well established statistical methods in the field which would enable to identify the time window/topography that maximally distinguished between the expected and the unexpected condition both for ERP and TF. Along the same lines, the authors could report the spatial correlation of the ERP/TF effects.

For the ERP analysis we used the standard electrodes typically analyzed for the Nc in order to replicate effects found in former research (Langeloh et al., 2020; see also, Kayhan et al., 2019; Reynolds and Richards, 2005; Webb et al., 2005). For the TF analyses we used the most conservative criterion, namely all scalp recorded electrodes and the whole time window from 0 to 2000 ms, such that we did not make any choice regarding time window or the electrodes (i.e., which could be corrected for against other choices). We have now made those choices clearer in the method section, and why we think that, under these condition a multiple comparison correction is not needed/applicable (p. 10). Regarding the spatial correlation of the ERP and TF effects, we explained in response to the first comment the very different nature of the TF decomposition of the ERP and ongoing oscillatory activity and also that these were found to be interdependent (i.e., uncorrelated). We hope that with the additional analysis included in response to this comment that this difference is much clearer now.

2) While I can see the reason why the authors chose to keep the baseline the same between the ERP and the TF analysis, for time frequency analysis it would be advisable to use a baseline amounting to a comparable time to the frequency of interest; and to use a period that does not encroach in the period of interest i.e., with a wavelet = 7 and a baseline -100:0 the authors are well into the period of interested.

The difficulty in choosing the baseline in the present study was two-fold. First, we were interested in the ERP and the change in neural oscillations upon the onset of an outcome picture within a continuous presentation of pictures, forming a sequence. Second, we wanted to use a similar baseline for both analyses, to make them comparable. Because the second picture (the picture before the outcome picture) also elicited both an ERP and an oscillatory response at ~ 4 Hz (see Additional Figure 2), we choose a baseline just before the onset of the outcome stimulus, from -100 to 0 ms. Also we agree that the possibility to take a longer and earlier baseline, in particular for the TF results would have been favorable, but still consider that the -100 to 0 ms is still the best choice for the present analysis. Notably, because we found an increase in theta oscillations and the critical difference relies on a higher theta rhythm in one compared to the other condition, the effects of the increase in theta, if they effected the baseline, this effect would counteract rather than increase the current effect. We now explain this choice in more detail (p.10).

Additional Figure 1. Display of the grand mean signals prior to the -100 to 0 baseline and outcome stimulus. (A) The time-frequency response across all scalp-recorded electrodes, as well as (B) the ERP at the central electrodes (Cz, C3, C4) across both conditions show a similar response to the 2. picture like the outcome picture. Thus a baseline just prior to the stimulus of interest was chosen, consistent for both analyses.

Reviewer #2:

The manuscript reports increases in theta power and lower NC amplitude in response to unexpected (vs. expected) events in 9-month-olds. The authors state that the observed increase in theta power is significant because it is in line with an existing theory that the theta rhythm is involved in learning in mammals. The topic is timely, the results are novel, the sample size is solid, the methods are sound as far as I can tell, and the use of event types spanning multiple domains (e.g. action, number, solidity) is a strength. The manuscript is short, well-written, and easy to follow.

1) The current version of the manuscript states that the reported findings demonstrate that the theta rhythm is involved in processing of prediction error and supports the processing of unexpected events in 9-month-old infants. However, what is strictly shown is that watching at least some types of unexpected events enhance theta rhythm in 9-month-old infants, i.e. an increase in the theta rhythm is associated with processing unexpected events in infants, which suggests that an increase in the theta rhythm is a possible neural correlate of prediction error in this age range. While the present novel findings are certainly suggestive, more data and/or analyses would be needed to corroborate/confirm the role of the observed infant theta rhythm in processing prediction error, or document whether and how this increase in the theta rhythm supports the processing of unexpected events in infants. (As an example, since eye-tracking data were collected, are trial-by-trial variations in theta power increases to unexpected outcomes related to how long individual infants looked to the unexpected outcome pictures?) If it is not possible to further confirm/corroborate the role of the theta rhythm with this dataset, then the discussion, abstract, and title should be revised to more closely reflect what the current data shows (as the wording of the conclusion currently does), and clarify how future research may test the hypothesis that the infant theta rhythm directly supports the processing of prediction error in response to unexpected events.

We would like to thank the reviewer for acknowledging the merit of the present research.

On the one hand, we have revised our manuscript and are now somewhat more careful with our conclusion, in particular with regard to the refinement of basic expectations. On the other hand, we consider the concept of “violation to expectation” (VOE), which is one of the most widely used concepts in infancy research, very closely linked to the concept of a prediction error processing, namely a predictive model is violated. In particular, we have made this conceptual link in a recent theoretical paper (Köster et al., 2020), and based on former theoretical considerations about the link between these two concepts (e.g., see Schubotz 2015; Prediction and Expectation). In particular, in the present study we used a set of four different domains of violation of expectation paradigms, which are among the best established domains of infants core knowledge (e.g., action, solidity, cohesion, number; cf. Spelke & Kinzler, 2007). It was our specific goal not to replicate, for another time, that infants possess expectations (i.e., make predictions) in these domains, but to “flip the coin around” and investigate infants’ prediction error more generally, independent of the specific domain. We have now made the conceptual link between VOE and prediction error processing more explicit in the introduction of the manuscript and also emphasize that we choose a variety of domains to obtain a more general neural marker for infant processing of prediction errors.

Having said this, indeed, we planned to assess and compare both infants gaze behavior and EEG response. Unfortunately, this was not very successful and the concurrent recording only worked for a limited number of infants and trials. This led us to the decision to make the eye-tracking study a companion study and to collect more eye-tracking data in an independent sample of infants after the EEG assessment was completed, such that a match between the two measures was not feasible. We now make this choice more explicit in the method section (p. 7). In addition, contrary to our basic assumption we did not find an effect in the looking time measure. Namely, there was no difference between expected and unexpected outcomes. We assume that this is due to the specificities of the current design that was rather optimized for EEG assessments: We used a high number of repetitions (64), with highly variable domains (4), and restricted the time window for potential looking time effects to 5 seconds, which is highly uncommon in the field and therefore not directly comparable with former studies.

Finally, besides the ample evidence from former studies using VOE paradigms, if it were not the unexpected vs. expected (i.e., unpredicted vs. predicted) condition contrast which explains the differences we found in the ERP and the theta response, there would need to be an alternative explanation for the differential responses in the EEG, which produce the hypothesized effects. (Please also note that there are many studies relying their VOE assumption on ERPs alone, here we have two independent measures suggesting that infants discriminated between those conditions.)

2) The current version of the manuscript states "The ERP effect was somewhat consistent across conditions, but the effect was mainly driven by the differences between expected and unexpected events in the action and the number domain (Figure S1). The results were more consistent across domains for the condition difference in the 4 - 5 Hz activity, with a peak in the unexpected-expected difference falling in the 4 - 5 Hz range across all electrodes (Figure S2)". However, the similarity/dissimilarity of NC and theta activity responses across domains was not quantified or tested. Looking at Figures S1 and S2, it is not that obvious to me that theta responses were more consistent across domains than NC responses. I understand that there were too few trials to formally test for any effect of domain (action, number, solidity, cohesion) on NC and theta responses, either alone or in interaction with outcome (expected, unexpected). It may still be possible to test for correlations of the topography and time-course of the individual average unexpected-expected difference in NC and theta responses across domains at the group level, or to test for an effect of outcome (expected, unexpected) in individual domains for subgroups of infants who contributed enough trials. Alternatively, claims of consistency across domains may be altered throughout, in which case the inability to test whether the theta and/or NC signatures of unexpected event processing found are consistent across domains (vs. driven by some domains) should be acknowledged as a limitation of the present study.

We agree that this statement rather reflected our intuition and would not surpass statistical analysis given the low number of trials. So we are happy to refrain from this claim and simply refer to the supplementary material for the interested reader and also mention this as a perspective for future research in the discussion (p. 12; p. 15).

As outlined in our previous response, it was also not our goal to draw conclusions about each single domain, but rather to present a diversity of stimulus types from different core knowledge domains to gain a more generalized neural marker for infants’ processing of unexpected, i.e., unpredicted events.

Reviewer #3:

General assessment:

In this manuscript, the authors bring up a contemporary and relevant topic in the field, i.e. theta rhythm as a potential biomarker for prediction error in infancy. Currently, the literature is rich on discussions about how, and why, theta oscillations in infancy implement the different cognitive processes to which they have been linked. Investigating the research questions presented in this manuscript could therefore contribute to fill these gaps and improve our understanding of infants' neural oscillations and learning mechanisms. While we appreciate the motivation behind the study and the potential in the authors' research aim, we find that the experimental design, analyses and conclusions based on the results that can be drawn thereafter, lack sufficient novelty and are partly problematic in their description and implementation. Below, we list our major concerns in more detail, and make suggestions for improvements of the current analyses and manuscript.

Summary of major concerns:

1) Novelty:

(a) It is unclear how the study differs from Berger et al., 2006 apart from additional conditions. Please describe this study in more detail and how your study extends beyond it.

We would like to thank the reviewers for emphasizing the timeliness and relevance of the study.

The critical difference between the present study and the study by Berger et al. 2006 was that the authors applied, as far as we understand this from Figure 4 and the method section of their study, the wavelet analysis to the ERP signal. In contrast, in the present study, we applied the wavelet analysis at the level of single trials. We now explain the difference between the two signals in more detail in the revised manuscript and also included an additional comparison between the evoked (i.e., ERP) and the ongoing (i.e., total) oscillatory response (for more details, please see the first response to the first comment of reviewer 1).

(b) Seemingly innovative aspects (as listed below), which could make the study stand out among previous literature, but are ultimately not examined. Consequently, it is also not clear why they are included.

-Relation between Nc component and theta.

-Consistency of the effect across different core knowledge domains.

-Consistency of the effect across the social and non-social domains.

-Link between infants looking at time behavior and theta.

We are thankful for these suggestions, which are closely related to the points raised by reviewer 1 and 2. With regard to the relation between the Nc and the theta response, we have now included a direct comparison of these signals (see Additional Figure 1, i.e., novel Figure S2; for details, please see the first response to the first comment of reviewer 1). Regarding the consistency of effects across domains, we have explained in response to point 1 by reviewer 2 that this was not the specific purpose of the present study, but we aimed at using a diversity of VOE stimuli to obtain a more general neural signature for infants’ prediction error processing, and explain this in more detail in the revised manuscript. Having said this, we agree that the question of consistency of effects between conditions is highly interesting, but we would not consider the data robust enough to confidently test these differences given the limited number of trials available per stimulus category. We now discuss this as a direction for future research (p. 15). Finally, we also agree with regard to the link between looking times and the theta rhythm. As also outlined in response to point 1 by reviewer 2 (paragraph 2), we initially had this plan, but did not succeed in obtaining a satisfactory number of trials in the dual recording of EEG and eye-tracking, which made us change these plans. This is now explained in detail in the method section (p. 7).

(c) The reason to expect (or not) a difference at this age, compared to what is known from adult neural processing, is not adequately explained.

-Potentially because of neural generators in mid/pre-frontal cortex? See Lines 144-146.

The overall aim of the present study was to identify the neural signature for prediction error processing in the infant brain, which has, to the best of our knowledge, not been done this explicitly and with a focus on the ongoing theta activity and across a variety of violations in infants’ core knowledge domains. Because we did not expect a specific topography of this effect, in particular across multiple domains, we included all electrodes in the analyses. We have now clarified this in the method section (p. 10).

(d) The study is not sufficiently embedded in previous developmental literature on the functionality of theta. That is, consider theta's role in error processing, but also the increase of theta over time of an experiment and it's link to cognitive development. See, for example: Braithwaite et al., 2020; Conejero et al., 2018; Adam et al., 2020.

We are thankful that the reviewer indicated these works and have now included them in the introduction and discussion. Closest to the present study is the study by Conejero et al., 2018. However, this study is also based on theta analyses of the ERP, not of the ongoing oscillatory response and it includes considerably older infants (i.e., 16-month-olds instead of 9-month-olds as in the present study).

2) Methodology:

(a) Design: It is unclear what exactly a testing session entails.

-Was the outcome picture always presented for 5secs? The methods section suggests that, but the introduction of the design and Figure 1 do not. This might be misleading. Please change in Figure 1 to 5sec if applicable.

Yes, the final images were shown for 5s in order to simultaneously assess infants’ looking times. However, we included trials in the EEG analysis if infants looked for 2s, so this is the more relevant info for the analysis. We now clarified this in the method section (p. 7) and have also added this info in the figure caption.

-Were infants' eye-movements tracked simultaneously to the EEG recording? If so, please present findings on their looking time and (if possible) pupil size. Also examine the relation to theta power. This would enhance the novelty and tie these findings to the larger looking time literature that the authors refer to in their introduction.

Yes, in response to the second reviewer (comment 1) we explained in more detail why the joint analysis of the EEG and looking time data was not possible: We planned to assess both, infants gaze behavior and EEG response. Unfortunately, this was not very successful and the dual recording only worked for a few infants and trials. This led us to collect more eye-tracking data after the EEG assessment was completed, such that a match between the two measures was not feasible. We now clarified this in the method section (p. 7).

(b) Analysis:

-In terms of extracting theta power information: The baseline of 100ms is extremely short for a comparison in the frequency domain, since it does not even contain half a cycle of the frequency of interest, i.e. 4Hz. We appreciate the thought to keep the baseline the same as in the ERP analysis (which currently is hardly focused on in the manuscript), but it appears problematic for the theta analysis. Also, if we understand the spectral analysis correctly, the window the authors are using to estimate their spectral estimates is largely overlapping between baseline and experimental window. The question arises whether a baseline is even needed here, or if a direct contrast between conditions might be better suited.

Please see our explanation about the choice of the baseline in our response to reviewer 1, comment 2. Because our stimulus sequences were highly variable, likely leading to highly variable overall theta activity, and our specific interest was in the change in theta activity upon the onset of the unexpected versus unpredicted outcome, we still consider it useful to take a baseline here. Also because this makes the study more closely comparable to the existing literature. We now clarified this in the method section (p. 9)

-In terms of statistical testing

-It appears that the authors choose the frequency band that will be entered in the statistical analysis from visual inspection of the differences between conditions. They write: "we found the strongest difference between 4 - 5 Hz (see lower panel of Figure 3). Therefore, and because this is the first study of this kind, we analyzed this frequency range." ll. 277-279). This approach seems extremely problematic since it poses a high risk for 'double-dipping'. This is crucial and needs to be addressed. For instance, the authors could run non-parametric permutation tests on the time-frequency domain using FDR correction or cluster-based permutation tests on the topography.

-Lack of examining time- / topographic specificity.

Please also note the sentence before this citation, which states our initial hypothesis: “While our initial proposal was to look at the difference in the 4 Hz theta rhythm between conditions (Köster et al., 2019), we found the strongest difference between 4 – 5 Hz (see lower panel of Figure 3).” Note that the hypothesis of 4 Hz can be clearly derived from our 2019 study. We would maintain that the center frequency we took for the analysis 4.5Hz (i.e., 4 – 5Hz) is very close to this original hypothesis and, considering that we applied a novel design and analyses in very young infants, could indeed hardly have fallen more closely to this initial proposal. The frequency choice is also underlined, as the reviewer remarks, by the consistency of this peak across domains, peaking at 4Hz (cohesion), 4.5Hz (action), and 5Hz (solidity, number). Importantly, please note that we have chosen the electrodes and time window very conservatively, namely by including the whole time period and all electrodes, which we now explain in more detail on p. 10. Please also see our response to reviewer 1, comment “1)”.

3) Interpretation of results:

(a) The authors interpret the descriptive findings of Figure S1 as illustration of the consistency of the results across the four knowledge domains. While we would partly agree with this interpretation based on column A of that figure (even though also there the peak shifts between domains), columns B and C do not picture a consistent pattern of data. That is, the topography appears very different between domains and so does the temporal course of the 4-5Hz power, with only showing higher power in the action and number domain, not in the other two. Since none of these data were compared statistically, any interpretation remains descriptive. Yet, we would like to invite the authors to critically reconsider their interpretation. You also might want to consider adding domain (action, number etc.) as a covariate to your statistical model.

We agree with the reviewers (reviewer 2 and reviewer 3) that our initial interpretation of the data regarding the consistency of effects across domains may have been too strong. Thus, in the revised version of the manuscript, we do not state that the TF analysis revealed more consistent results. Given that the analysis was based on a different subsample and highly variable in trial numbers, we did not enter them as a covariate in the statistical model.

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

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Reply to the reviewers

Manuscript number: RC-2025-03220

Corresponding author(s): Ryusuke Niwa, Yuko Shimada-Niwa, and Wei Sun

Dear Editors,

We are pleased to submit our revised manuscript of RC-2025-03220R. The reviewers’ comments from Review Commons are presented in italic.

For submission of our current revised manuscript, we provide two Word files, which are the “clean” and “Track-and-Change” files. Page and line numbers described below correspond to those of the “clean” file. The “Track-and-Change” file might be helpful for Reviewers to find what we have changed for the current revision.

We hope that the revised version is now suitable for the next stage of evaluation.

Sincerely,

Ryusuke Niwa, Yuko Shimada-Niwa, and Wei Sun

1. General Statements [optional]

We sincerely thank the reviewers for their thoughtful feedback on our initial submission. Experiments that we will conduct and the revisions on the manuscript that have already been incorporated are detailed below in the point-by-point response. For this revised submission, two versions of the manuscript are provided: a clean copy and a tracked-changes file. Page and line numbers mentioned below refer to the clean version, while the tracked-changes file is intended to help reviewers easily identify the revisions made.

In preparing the revision plan, we have included additional data, some of which were generated in collaboration with new contributors. Accordingly, we would like to propose adding Yuichi Shichino and Shintaro Iwasaki as co-authors to acknowledge their contributions.

2. Description of the planned revisions__ __

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- Also, the authors show that two different RNAi lines for NudC give the same defects - it would be good to know if the RNAi lines target the same or different sequences in the NudC transcripts. Alternatively, it would be equally good to show that trans-allelic combinations of NudC mutants have the same defects in the prothoracic glands and the salivary glands as the RNAi. Instead, they examine only overall body size, developmental delays and lethality in the trans-hetero allelic NudC mutants.

Author response:

In response to the second part of the criticism, we will further validate the observed phenotypes by examining tissue and nuclear size, chromosomal structure, and the levels of Fibrillarin and RpS6 proteins in the prothoracic glands and salivary glands of NudC mutants.

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- It would be quite helpful to characterize the "5 blob" and "shortened polytene chromosome arm" defects shown in Figure 2 and Figure 6. Are these partially polytenized chromosomes or are large sections of the chromosomes missing or just underreplicated? What do the chromosomes look like if you lyse the nuclei, spread the chromosomes and stain with DAPI or Hoechst - this is a pretty standard practice and would reveal much more about the structure of the polytene chromosomes.

Author response:

To address these structural concerns more clearly, we plan to apply established protocols to obtain higher-resolution images and gather more detailed information on chromosome morphology.

__ - Discussion, line 468. I don't think the authors have provided evidence of DNA damage. With the experiments they have shown, the chromosomes look abnormal - not clear what is abnormal.

Author response:

To further confirm DNA damage in NudC knockdown salivary gland cells, we plan to perform a TUNEL assay, which detects DNA fragmentation associated with damage.

We would like to note that, in the current manuscript, we have shown that depletion of NudC, eIF5, RpLP0-like, or Nopp140 increased γH2Av levels, suggesting activation of the DNA damage response (Figures 6B and 6C).

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*The authors claim that NudC has a dual role as a cell cycle/cytoskeleton regulator and as a ribosome biogenesis factor. However, because NudC knockdown reduces nuclear size and ploidy (Figures 1F and 2H-2I), the authors cannot exclude that decreased rDNA dosage and nucleolar volume contribute to reduced rRNA signals and that the effects seen are due to a NudC involvement in endoreplication, the rRNA reduction being a consequence of lower polyploidy. Different allelic combinations of NudC induce larval growth defects (Figure S5), consistent with a NudC role in endoreplication. To circumvent this, the authors could genetically modulate endocycle progression (e.g., E2F or Fzr overexpression) in the NudC RNAi background to test whether inducing endoreplication rescues rRNA production and nucleolar volume. This would establish causality between the endocycle state and rRNA output and clarify whether NudC's primary role is in RiBi or endocycle control. *

Author response: In response to Reviewer #2’s suggestion, we plan to genetically modify the progression of the endocycle by inducing continuous expression of Cyclin E (CycE), E2F1, and Fzr in NudC RNAi salivary glands to test whether promoting endoreplication can restore rRNA production and nucleolar volume.

In fact, we have attempted to rescue the developmental arrest in animals with NudC-deficient prothoracic glands (PGs) by inducing continuous expression of CycE. Two constructs, UAS-CycE-1 (BDSC#30725) and UAS-CycE-2 (BDSC#30924), were used. UAS-CycE-1 has previously been shown to rescue developmental arrest in PG-specific TOR loss-of-function animals (Ohhara, Kobayashi, and Yamanaka. PLoS Genetics 13 (1): e1006583, 2017). We introduced each construct into NudC knockdown PGs. However, continuous expression of CycE did not restore development (Figure A as shown below), suggesting that NudC functions in the polyploid cells extend beyond endocycle regulation. We do not currently plan to include the PG data shown in Figure A in the revised manuscript. We will evaluate whether it would be meaningful to present PG data alongside salivary gland results once we have obtained and analyzed data from the salivary gland rescue experiment.

__Figure A. _Survival and developmental progression following continuous expression of CycE._ __Control (phtm>dicer2, +), NudC knockdown (phtm>dicer2, NudC RNAi), and NudC RNAi + CycE (phtm>dicer2, NudC RNAi, CycE) flies were analyzed at 10 days after hatching (10 dAH). Dead indicates dead larvae; L3 denotes third-instar larvae. Sample sizes (number of flies) are shown below each bar.

__

*The conclusion that NudC maintains rRNA levels is derived from salivary gland RNAi phenotypes with strong reductions in ITS1/ITS2 and 18S/28S signals (Figure 4B-4K) and reduced 28S by Northern (Figure 4L), plus corroboration in fat body cells (Figure S7). The authors verified knockdown using two independent RNAi lines for growth phenotypes and NudC::GFP reduction (Figure S2) and generated a UAS-FLAG::NudC transgene (Key Resources), but rRNA measurements were reported for only one RNAi line without rescue. Rescue of the rRNA phenotype by transgenic NudC re-expression, or replication of the rRNA decrease with a second, non-overlapping RNAi, would directly attribute the effect to NudC. In the absence of these standard validation controls, an off-target explanation remains plausible. *

Author response:

We plan to analyze rRNA FISH signals in salivary glands and fat bodies using a second, non-overlapping RNAi strain to confirm the reproducibility of the observed effects.

__ - The authors report in Fig. 2 elevated γH2Av in SG cells upon NudC knockdown and interpret this as evidence of chromosome destabilization. They also state that apoptosis is not observed in Fig S10. However, the increase in γH2Av could reflect transient or early apoptotic events or other stress responses triggered by NudC depletion, rather than direct defects in endoreplication or genome stability. I suggest that the authors clarify this important point, for example, by co-expressing apoptotic inhibitors such as P35, or by using the TUNEL assay, which is more sensitive than anti-Caspase3 or Dcp1 antibodies.

Author response:

We plan to perform a TUNEL assay on salivary gland cells to evaluate apoptosis associated with NudC depletion.

__ - Activation of the JNK pathway is often accompanied by apoptosis. It would strengthen the conclusions if the authors included a positive control to confirm that apoptosis is not induced under these experimental conditions, ensuring that the observed effects are specific to autophagy and not confounded by cell death.

Author response:

We will analyze pJNK and autophagy levels in animals expressing a constitutively-active form of hemipterous (hep) (hep[CA] ) under the control of fkh-GAL4 driver as a positive control. hep encodes the Drosophila JNK kinase, and it is well established that forced expression of hep[CA] induces JNK phosphorylation and activation.

__ - In Figure S1, reduction of NudC in the fat body appears to induce a starvation-like phenotype, suggesting a potential impairment of metabolic or nutrient-sensing pathways. It would be important to determine whether modulation of nutrient-responsive signaling could rescue this phenotype. Specifically, have the authors examined whether activation of the TOR or PI3K pathways mitigates the effects of NudC knockdown? Assessing pathway activity (e.g., via phospho-S6K or phospho-Akt levels) or performing genetic rescue experiments with pathway activators could clarify whether the observed phenotypes are mediated through disrupted nutrient signaling rather than a secondary effect of general cellular stress. Such analyses could also provide a mechanistic explanation for the increased autophagy observed in these cells.

Author response:

1. We will analyze phospho-S6K levels in salivary glands and fat bodies by immunostaining.
2. To activate the TOR pathway in NudC RNAi fat bodies, we will overexpress Rheb, an established upstream activator of the TOR pathway in Drosophila, which has been shown to robustly increase TOR signaling and S6K phosphorylation.

   __ - The current images of autophagic vesicles in the SG in Fig. 8B are not clearly visible and quantified. Considering the large size of these polyploid cells, higher-resolution images or alternative imaging approaches should be presented to better visualize and quantify autophagy. This would make the conclusions regarding enhanced autophagy more convincing. In addition, this data could be further strengthened by expanding the analysis of autophagy to other cell types. For example, examining autophagy in fat body cells, where autophagy plays a primary physiological role associated with rRNA accumulation (Fig. S7), rather than a reduction like in SG (Fig. 4), could provide a useful comparison for the function of NudC between polyploid cells.

Author response:

In response to the second part of the reviewer’s comment, we will conduct additional experiments using anti-Atg8a immunostaining and/or LysoTracker staining to analyze autophagy in NudC RNAi fat bodies and prothoracic glands. These experiments will help further characterize the cellular responses associated with NudC depletion.

3. Description of the revisions that have already been incorporated in the transferred manuscript

__

-The title is a bit problematic since they haven't shown that NudC doesn't also affect normal mitotic cells - they only look at polyploid cells, but that doesn't mean normal mitotic cells are not also affected.

Author response:

In response to the suggestion from Reviewer #1, we have revised the title from “NudC moonlights in ribosome biogenesis and homeostasis in Drosophila melanogaster polyploid cells” to “NudC moonlights in ribosome biogenesis and homeostasis in polyploid cells of Drosophila melanogaster” to place greater emphasis on “polyploid cells.”

Regarding mitotic cells, we have added new data in the revised manuscript (Figure S7; lines 249–256 and 417–418) demonstrating that NudC regulates apoptosis and stress responses in mitotic imaginal wing disc cells. However, as the main focus of our study remains polyploid cells, we have chosen to retain the emphasis in the title.

__

- Also, the authors show that two different RNAi lines for NudC give the same defects - it would be good to know if the RNAi lines target the same or different sequences in the NudC transcripts. Alternatively, it would be equally good to show that trans-allelic combinations of NudC mutants have the same defects in the prothoracic glands and the salivary glands as the RNAi. Instead, they examine only overall body size, developmental delays and lethality in the trans-hetero allelic NudC mutants.

Author response:

In response to the first half of criticism, the two RNAi lines used for NudC target distinct sequences. We have added the corresponding RNAi target sites to Figure S4A for clarity.

__

- Results: Lines 261 - 266. Seeing electron dense structures in TEMs and seeing increased Me31B staining by confocal imaging in the cytoplasm is insufficient evidence that the electron dense structures are P-bodies. They could be the P-bodies but they could also be aggregated ribosomes; there is insufficient evidence to "confirm" that they are P-bodies - maybe just say "suggests".

Author response:

In response to Reviewer #1’s suggestion, we have revised lines 261–262 to avoid using the word "confirm." The new sentence reads: “Immunostaining with the P-body marker Me31B reveals numerous cytoplasmic P-bodies in NudC-deficient SG cells,” which appears in lines 293–295.

__

- Abstract, lines 28 - 31. I think this gene has been identified before. The authors probably want to say they have discovered a role for this gene in RiBi.

Author response:

We have followed Reviewer #1’s suggestion and revised the sentence in lines 35–37 to: “In this study, we discovered a role for the gene NudC (nuclear distribution C, dynein complex regulator) in RiBi within polyploid cells of Drosophila melanogaster larvae.”

__

- Introduction, line 66. The protein is imported into the nucleus, where it localizes to the nucleolus - technically the protein is not imported into the nucleolus.

Author response:

To correct the misrepresentation in line 66, we have revised the sentence to: “RP mRNAs are synthesized by RNA polymerase II, and exported to the cytoplasm for translation. Then, RPs are imported into the nucleus, where they localize to the nucleolus.” in lines 70–73.

__ - Introduction, line 70. To be comprehensive in the description of ribosome biogenesis, the authors may want to mention that the 40S and 60S subunits are then exported from the nucleus and form the 80S subunit in the cytoplasm during translation.

Author response:

To improve the representation, we have revised the sentences in lines 73 – 78 as follows: “Within the nucleolus, rRNAs and RPs assemble into pre-40S and pre-60S subunits. immature versions of the small (40S) and large (60S) subunits, respectively, that undergo maturation with numerous ribosome biogenesis factors (RBFs) (Greber, 2016). The 40S and 60S subunits are then transported separately to the cytoplasm, where they combine to form functional 80S ribosomes, capable of sustaining protein synthesis (Pelletier et al., 2018).”

__ - Introduction, line 98. May want to cite paper showing that Minute mutations turn out to be mutations in individual ribosomal protein genes.

Author response:

As Reviewer #1 suggested, we have cited two, Marygold et al. (2007) entitled “The ribosomal protein genes and Minute loci of Drosophila melanogaster” and Recasens-Alvarez et al. (2021) entitled “Ribosomopathy-associated mutations cause proteotoxic stress that is alleviated by TOR inhibition” along with He et al. (2015). The inappropriate citation to Brehme (1939) has been removed.

__ - Results, lines 292. Since they didn't knock down NudC in the fat body cells in this experiment, this comment seems irrelevant.

Author response:

We would like to clarify that the phenotype observed with fkh-GAL4-driven NudC RNAi was specific to salivary glands, and no obvious phenotypes were detected in the surrounding fat body cells, which do not express fkh-GAL4. In this context, the adjacent fat body cells serve as an internal control.

In the revised manuscript, the sentence has been rewritten as: “In contrast, the fat body cells surrounding NudC-deficient SGs did not show this reduction (Figure S9),” in lines 323–324.

__ - Figure 6A. Hoechst is misspelled.

__

- Fig. 2 I - Hoeschest should be Hoescht.

Author response:

We have fixed the error.

__ *- Given that prothoracic gland (PG) size influences ecdysone production, the finding that NudC knockdown alters PG cell size, morphology, and cytoskeletal organization raises the possibility that ecdysone synthesis or signaling may also be affected. This, in turn, could explain the delayed maturation phenotype observed in Figure 1. I recommend testing whether ectopic activation of ecdysone signaling, for instance through 20-hydroxyecdysone (20E) supplementation, can rescue the defects in PG size and developmental timing. Such an experiment would strengthen the link between NudC function, PG morphology, and ecdysone-dependent developmental progression. *

Author response:

We have conducted experiments showing that developmental defects in NudC RNAi animals can be partially rescued by administering 20E. Approximately 32% of NudC RNAi larvae fed with 20E completed pupariation. These new data have been added to Figure S1B and are described in the main text (lines 165-168).

Regarding PG size, our experiments show that PG growth remains inhibited following 20E administration (Figure B as shown below). This observation indicates that treatment with exogenous 20E does not restore PG growth in NudC RNAi animals, suggesting that other factors may be required for normal PG development beyond ecdysone supplementation.

Because this analysis is not the main focus of our manuscript, we currently plan not to include these data in the revised manuscript.

Figure B. Prothoracic gland (PG) size ____after 20E administration.

To assess whether 20E supplementation could restore PG size, control (phtm>dicer2, +) and NudC RNAi (phtm>dicer2, NudC RNAi) larvae were transferred at 60 hours after hatching (hAH) to standard medium containing 20E dissolved in 100% ethanol. Control groups were transferred to medium containing the same volume of 100% ethanol at the same time point. PG size was quantified at the wandering stage. Sample sizes (number of glands) are shown below each bar. Bars represent mean ± SD. **p * *

__ - Additionally, qRT-PCR can be performed to assess the expression levels of ecdysone precursors or target genes in whole larvae, serving as a readout of ecdysone activity, including dilp8, which is usually upregulated when ecdysone levels are reduced.

Author response: To investigate ecdysone biosynthesis, Halloween genes including nvd, spok, sro, phm, dib, and sad were measured by conducting qRT-PCR. In NudC RNAi animals, nvd, sro and phm were suppressed at late L3 stage, indicating that NudC in the PG is required for ecdysone biosynthesis. The new data are described in Figure S1A and in the main text (lines 159-164) in the revised manuscript.

__ - The current images of autophagic vesicles in the SG in Fig. 8B are not clearly visible and quantified. Considering the large size of these polyploid cells, higher-resolution images or alternative imaging approaches should be presented to better visualize and quantify autophagy. This would make the conclusions regarding enhanced autophagy more convincing.

Author response:

Regarding the image quality issue, we have provided improved images of anti-Atg8a immunostaining in the salivary gland mosaic clones (Figure 8B) and included additional data from SG-specific knockdown cells (Supplemental Figures S13A-S13F) to provided quantitative results.

__ - Furthermore, including experiments in other cell types, such as imaginal disc cells, where apoptosis is more readily induced, would help determine whether the effects of NudC knockdown are specific to polyploid cells or are more broadly applicable.

Author response: We found that apoptosis was observed in NudC RNAi wing discs. In the revised manuscript, we have included this data in Figure S7 and referenced it in the main text (lines 249–256).

4. Description of analyses that authors prefer not to carry out

__ - Results, lines 285 to 298. In situs with multiple probes that detect all parts of both the pre-rRNA and processed rRNA indicate that all are down in the SG in NudC knockdowns, but that the 18S and 28S rRNAs are down the internal transcribed spacers go up - can the authors explain or hypothesize how this could happen?

Author response:

As Reviewer #1 indicated, we indeed observed that internal transcribed spacer (ITS) levels decrease in NudC knockdown salivary glands, but increase in knockdown fat bodies. Our hypothesis is that, as noted in the Discussion (lines 529–534), ribosome abundance is typically linked to protein synthesis. Salivary gland cells, which are highly active in protein production, may be particularly sensitive to disruptions in ribosome biogenesis. Therefore, NudC may maintain appropriate levels of rRNA with its impact varying according to the specific regulatory mechanisms of each cell type. We do not have a further explanation for this phenomenon, and therefore we have retained the original sentences without adding new ones.

__ - The data presented in Fig 4 show that NudC knockdown reduces pre-rRNA (ITS1/ITS2) and mature 18S/28S rRNAs in a tissue-specific manner. However, it remains unclear whether these reductions have functional consequences for ribosome assembly and translation. I recommend that the authors perform polysome profiling or an equivalent assay to assess the impact of NudC loss on actively translating ribosomes. This approach would provide a quantitative readout of translation efficiency and clarify whether the observed rRNA defects lead to impaired protein synthesis. Additionally, polysome profiling could help explain the tissue-specific differences observed between salivary glands and fat body cells.

Author response:

We performed ribosome fractionation using wild-type salivary glands and repeated the experiment three times with 56–62 gland pairs per sample. As shown in Figure C, the polyribosome peaks (grey lines) are not prominent, indicating that a much larger number of glands would be required for robust polysome profiling. Given that NudC RNAi salivary glands are significantly smaller than wild-type glands, collecting enough tissue for equivalent profiling would be technically difficult. Therefore, we concluded that obtaining sufficient RNAi samples for polysome profiling is extremely challenging, and these data have not been included in the revised manuscript.

On the other hand, we would like to emphasize that we observed a significant reduction in O-propargyl puromycin (OPP) labeling in NudC-deficient salivary gland cells (Figure 3B), which provides strong evidence for reduced translational activity.

__Figure C. Ribosomal fraction profiles of wild-type salivary glands. __Salivary glands from the late L3 larvae were dissected for analysis. Polyribosome peaks are indicated in grey. The number of salivary gland pairs used for each sample is shown above each bar.

Author Response

Reviewer #1:

Hutchings et al. report an updated cryo-electron tomography study of the yeast COP-II coat assembled around model membranes. The improved overall resolution and additional compositional states enabled the authors to identify new domains and interfaces--including what the authors hypothesize is a previously overlooked structural role for the SEC31 C-Terminal Domain (CTD). By perturbing a subset of these new features with mutants, the authors uncover some functional consequences pertaining to the flexibility or stability of COP-II assemblies.

Overall, the structural and functional work appears reliable, but certain questions and comments should be addressed prior to publication. However, this reviewer failed to appreciate the conceptual advance that warrants publication in a general biology journal like eLIFE. Rather, this study provides a valuable refinement of our understanding of COP-II that I believe is better suited to a more specialized, structure-focused journal.

We agree that in our original submission our description of the experimental setup, indeed similar to previous work, did not fully capture the novel findings of this paper. Rather than being simply a higher resolution structure of the COPII coat, in fact we have discovered new interactions in the COPII assembly network, and we have probed their functional roles, significantly changing our understanding of the mechanisms of COPII-mediated membrane curvature. In the revised submission we have included additional genetic data that further illuminate this mechanism, and have rewritten the text to better communicate the novel aspects of our work.

Our combination of structural, functional and genetic analyses goes beyond refining our textbook understanding of the COPII coat as a simple ‘adaptor and cage’, but rather it provides a completely new picture of how dynamic regulation of assembly and disassembly of a complex network leads to membrane remodelling.

These new insights have important implications for how coat assembly provides structural force to bend a membrane but is still able to adapt to distinct morphologies. These questions are at the forefront of protein secretion, where there is debate about how different types of carriers might be generated that can accommodate cargoes of different size.

Major Comments: 1) The authors belabor what this reviewer thinks is an unimportant comparison between the yeast reconstruction of the outer coat vertex with prior work on the human outer coat vertex. Considering the modest resolution of both the yeast and human reconstructions, the transformative changes in cryo-EM camera technology since the publication of the human complex, and the differences in sample preparation (inclusion of the membrane, cylindrical versus spherical assemblies, presence of inner coat components), I did not find this comparison informative. The speculations about a changing interface over evolutionary time are unwarranted and would require a detailed comparison of co-evolutionary changes at this interface. The simpler explanation is that this is a flexible vertex, observed at low resolution in both studies, plus the samples are very different.

We do agree that our proposal that the vertex interface changes over evolutionary time is speculative and we have removed this discussion. We agree that a co-evolutionary analysis will be enlightening here, but is beyond the scope of the current work.

We respectfully disagree with the reviewer’s interpretation that the difference between the two vertices is due to low resolution. The interfaces are clearly different, and the resolutions of the reconstructions are sufficient to state this. The reviewer’s suggestion that the difference in vertex orientation might be simply attributable to differences in sample, such as inclusion of the membrane, cylindrical versus spherical morphology, or presence of inner coat components were ruled out in our original submission: we resolved yeast vertices on spherical vesicles (in addition to those on tubes) and on membrane-less cages. These analyses clearly showed that neither the presence of a membrane, nor the change in geometry (tubular vs. spherical) affect vertex interactions. These experiments are presented in Supplementary Fig 4 (Supplementary Fig. 3 in the original version). Similarly, we discount that differences might be due to the presence or absence of inner coat components, since membrane-less cages were previously solved in both conditions and are no different in terms of their vertex structure (Stagg et al. Nature 2006 and Cell 2008).

We believe it is important to report on the differences between the two vertex structures. Nevertheless, we have shifted our emphasis on the functional aspects of vertex formation and moved the comparison between the two vertices to the supplement.

2) As one of the major take home messages of the paper, the presentation and discussion of the modeling and assignment of the SEC31-CTD could be clarified. First, it isn't clear from the figures or the movies if the connectivity makes sense. Where is the C-terminal end of the alpha-solenoid compared to this new domain? Can the authors plausibly account for the connectivity in terms of primary sequence? Please also include a side-by-side comparison of the SRA1 structure and the CTD homology model, along with some explanation of the quality of the model as measured by Modeller. Finally, even if the new density is the CTD, it isn't clear from the structure how this sub-stoichiometric and apparently flexible interaction enhances stability. Hence, when the authors wrote "when the [CTD] truncated form was the sole copy of Sec31 in yeast, cells were not viable, indicating that the novel interaction we detect is essential for COPII coat function." Maybe, but could this statement be a leap to far? Is it the putative interaction essential, or is the CTD itself essential for reasons that remain to be fully determined?

The CTD is separated from the C-terminus of the alpha solenoid domain by an extended domain (~350 amino acids) that is predicted to be disordered, and contains the PPP motifs and catalytic fragment that contact the inner coat. This is depicted in cartoon form in Figures 3A and 7, and discussed at length in the text. This arrangement explains why no connectivity is seen, or expected. We could highlight the C-terminus of the alpha-solenoid domain to emphasize where the disordered region should emerge from the rod, but connectivity of the disordered domain to the CTD could arise from multiple positions, including from an adjacent rod.

The reviewer’s point about the essentiality of the CTD being independent of its interaction with the Sec31 rod, is an important one. The basis for our model that the CTD enhances stability or rigidity of the coat is the yeast phenotype of Sec31-deltaCTD, which resembles that of a sec13 null. Both mutants are lethal, but rescued by deletion of emp24, which leads to more easily deformable membranes (Čopič et al. Science 2012). We agree that even if this model is true, the interaction of the CTD with Sec31 that our new structure reveals is not proven to drive rigidity or essentiality. We have tempered this hypothesis and added alternative possibilities to the discussion.

We have included the SRA1 structure in Supplementary Fig 5, as requested, and the model z-score in the Methods. The Z-score, as calculated by the proSA-web server is -6.07 (see figure below, black dot), and falls in line with experimentally determined structures including that of the template (PDB 2mgx, z-score = -5.38).

3) Are extra rods discussed in Fig. 4 are a curiosity of unclear functional significance? This reviewer is concerned that these extra rods could be an in vitro stoichiometry problem, rather than a functional property of COP-II.

This is an important point, that, as we state in the paper, cannot be answered at the moment: the resolution is too low to identify the residues involved in the interaction. Therefore we are hampered in our ability to assess the physiological importance of this interaction. We still believe the ‘extra’ rods are an important observation, as they clearly show that another mode of outer coat interaction, different from what was reported before, is possible.

The concern that interactions visualised in vitro might not be physiologically relevant is broadly applicable to structural biology approaches. However, our experimental approach uses samples that result from active membrane remodelling under near-physiological conditions, and we therefore expect these to be less prone to artefacts than most in vitro reconstitution approaches, where proteins are used at high concentrations and in high salt buffer conditions.

4) The clashsccore for the PDB is quite high--and I am dubious about the reliability of refining sidechain positions with maps at this resolution. In addition to the Ramchandran stats, I would like to see the Ramachandran plot as well as, for any residue-level claims, the density surrounding the modeled side chain (e.g. S742).

The clashscore is 13.2, which, according to molprobity, is in the 57th percentile for all structures and in the 97th for structures of similar resolutions. We would argue therefore that the clashscore is rather low. In fact, the model was refined from crystal structures previously obtained by other groups, which had worse clashscore (17), despite being at higher resolution. Our refinement has therefore improved the clashscore. During refinement we have chosen restraint levels appropriate to the resolution of our map (Afonine et al., Acta Cryst D 2018)

The Ramachandran plot is copied here and could be included in a supplemental figure if required. We make only one residue-level claim (S742), the density for which is indeed not visible at our resolution. We claim that S742 is close to the Sec23-23 interface, and do not propose any specific interactions. Nevertheless we have removed reference to S742 from the manuscript. We included this specific information because of the potential importance of this residue as a site of phosphorylation, thereby putting this interface in broader context for the general eLife reader.

Minor Comments:

1) The authors wrote "To assess the relative positioning of the two coat layers, we analysed the localisation of inner coat subunits with respect to each outer coat vertex: for each aligned vertex particle, we superimposed the positions of all inner coat particles at close range, obtaining the average distribution of neighbouring inner coat subunits. From this 'neighbour plot' we did not detect any pattern, indicating random relative positions. This is consistent with a flexible linkage between the two layers that allows adaptation of the two lattices to different curvatures (Supplementary Fig 1E)." I do not understand this claim, since the pattern both looks far from random and the interactions depend on molecular interactions that are not random. Please clarify.

We apologize for the confusion: the pattern of each of the two coats are not random. Our sentence refers to the positions of inner and outer coats relative to each other. The two lattices have different parameters and the two layers are linked by flexible linkers (the 350 amino acids referred to above). We have now clarified the sentence.

2) Related to major point #1, the author wrote "We manually picked vertices and performed carefully controlled alignments." I do now know what it means to carefully control alignments, and fear this suggests human model bias.

We used different starting references for the alignments, with the precise aim to avoid model bias. For both vesicle and cage vertex datasets, we have aligned the subtomograms against either the vertex obtained from tubules, or the vertex from previously published membrane-less cages. In all cases, we retrieved a structure that resembles the one on tubules, suggesting that the vertex arrangement we observe isn’t simply the result of reference bias. This procedure is depicted in Supplementary Fig 4 (Supplementary Fig. 3 in the original manuscript), but we have now clarified it also in the methods section.

3) Why do some experiments use EDTA? I may be confused, but I was surprised to see the budding reaction employed 1mM GMPPNP, and 2.5mM EDTA (but no Magnesium?). Also, for the budding reaction, please replace or expand upon the "the 10% GUV (v/v)" with a mass or molar lipid-to-protein ratio.

We regret the confusion. As stated in the methods, all our budding reactions are performed in the presence of EDTA and Magnesium, which is present in the buffer (at 1.2 mM). The reason is to facilitate nucleotide exchange, as reported and validated in Bacia et al., Scientific Reports 2011.

Lipids in GUV preparations are difficult to quantify. We report the stock concentrations used, but in each preparation the amount of dry lipid that forms GUVs might be different, as is the concentration of GUVs after hydration. However since we analyse reactions where COPII proteins have bound and remodelled individual GUVs, we do not believe the protein/lipid ratio influences our structures.

4) Please cite the AnchorMap procedure.

We cite the SerialEM software, and are not aware of other citations specifically for the anchor map procedure.

5) Please edit for typos (focussing, functionl, others)

Done

Reviewer #2:

The manuscript describes new cryo-EM, biochemistry, and genetic data on the structure and function of the COPII coat. Several new discoveries are reported including the discovery of an extra density near the dimerization region of Sec13/31, and "extra rods" of Sec13/31 that also bind near the dimerization region. Additionally, they showed new interactions between the Sec31 C-terminal unstructured region and Sec23 that appear to bridge multiple Sec23 molecules. Finally, they increased the resolution of the Sec23/24 region of their structure compared to their previous studies and were able to resolve a previously unresolved L-loop in Sec23 that makes contact with Sar1. Most of their structural observations were nicely backed up with biochemical and genetic experiments which give confidence in their structural observations. Overall the paper is well-written and the conclusions justified.

However, this is the third iteration of structure determination of the COPII coat on membrane with essentially the same preparation and methods. Each time, there has been an incremental increase in resolution and new discoveries, but the impact of the present study is deemed to be modest. The science is good, but it may be more appropriate for a more specialized journal. Areas of specific concern are described below.

As described above, we respectfully disagree with this interpretation of the advance made by the current work. This work improves on previous work in many aspects. The resolution of the outer coat increases from over 40A to 10-12A, allowing visualisation of features that were not previously resolved, including a novel vertex arrangement, the Sec31 CTD, and the outer coat ‘extra rods’. An improved map of the inner coat also allows us to resolve the Sec23 ‘L-loop’. We would argue that these are not just extra details, but correspond to a suite of novel interactions that expand our understanding of the complex COPII assembly network. Moreover, we include biochemical and genetic experiments that not only back up our structural observations but bring new insights into COPII function. As pointed out in response to reviewer 1, we believe our work contributes a significant conceptual advance, and have modified the manuscript to convey this more effectively.

1) The abstract is vague and should be re-written with a better description of the work.

We have modified the abstract to specifically outline what we have done and the major new discoveries of this paper.

2) Line 166 - "Surprisingly, this mutant was capable of tubulating GUVs". This experiment gets to one of the fundamental unknown questions in COPII vesiculation. It is not clear what components are driving the membrane remodeling and at what stages during vesicle formation. Isn't it possible that the tubulation activity the authors observe in vitro is not being driven at all by Sec13/31 but rather Sec23/24-Sar1? Their Sec31ΔCTD data supports this idea because it lacks a clear ordered outer coat despite making tubules. An interesting experiment would be to see if tubules form in the absence of all of Sec13/31 except the disordered domain of Sec31 that the authors suggest crosslinks adjacent Sec23/24s.

This is an astute observation, and we agree with the reviewer that the source of membrane deformation is not fully understood. We favour the model that budding is driven significantly by the Sec23-24 array. To further support this, we have performed a new experiment, where we expressed Sec31ΔN in yeast cells lacking Emp24, which have more deformable membranes and are tolerant to the otherwise lethal deletion of Sec13. While Sec31ΔN in a wild type background did not support cell viability, this was rescued in a Δemp24 yeast strain, strongly supporting the hypothesis that a major contributor to membrane remodelling is the inner coat, with the outer coat becoming necessary to overcome membrane bending resistance that ensues from the presence of cargo. We now include these results in Figure 1.

However, we must also take into account the results presented in Fig. 6, where we show that weakening the Sec23-24 interface still leads to budding, but only if Sec13-31 is fully functional, and that in this case budding leads to connected pseudo-spherical vesicles rather than tubes. When Sec13-31 assembly is also impaired, tubes appear unstructured. We believe this strongly supports our conclusions that both inner and outer coat interactions are fundamental for membrane remodelling, and it is the interplay between the two that determines membrane morphology (i.e. tubes vs. spheres).

To dissect the roles of inner and outer coats even further, we have done the experiment that the reviewer suggests: we expressed Sec31768-1114, but the protein was not well-behaved and co-purified with chaperones. We believe the disordered domain aggregates when not scaffolded by the structured elements of the rod. Nonetheless, we used this fragment in a budding reaction, and could not see any budding. We did not include this experiment as it was inconclusive: the lack of functionality of the purified Sec31 fragment could be attributed to the inability of the disordered region to bind its inner coat partner in the absence of the scaffolding Sec13-31 rod. As an alternative approach, we have used a version of Sec31 that lacks the CTD, and harbours a His tag at the N-terminus (known from previous studies to partially disrupt vertex assembly). We think this construct is more likely to be near native, since both modifications on their own lead to functional protein. We could detect no tubulation with this construct by negative stain, while both control constructs (Sec31ΔCTD and Nhis-Sec31) gave tubulation. This suggests that the cross-linking function of Sec31 is not sufficient to tubulate GUV membranes, but some degree of functional outer coat organisation (either mediated by N- or C-terminal interactions) is needed. It is also possible that the lack of outer coat organisation might lead to less efficient recruitment to the inner coat and cross-linking activity. We have added this new observation to the manuscript.

3) Line 191 - "Inspecting cryo-tomograms of these tubules revealed no lozenge pattern for the outer 192 coat" - this phrasing is vague. The reviewer thinks that what they mean is that there is a lack of order for the Sec13/31 layer. Please clarify.

The reviewer is correct, we have changed the sentence.

4) Line 198 - "unambiguously confirming this density corresponds to 199 the CTD." This only confirms that it is the CTD if that were the only change and the Sec13/31 lattice still formed. Another possibility is that it is density from other Sec13/31 that only appears when the lattice is formed such as the "extra rods". One possibility is that the density is from the extra rods. The reviewer agrees that their interpretation is indeed the most likely, but it is not unambiguous. The authors should consider cross-linking mass spectrometry.

We have removed the word ‘unambiguously’, and changed to ‘confirming that this density most likely corresponds to the CTD’. Nonetheless, we believe that our interpretation is correct: the extra rods bind to a different position, and themselves also show the CTD appendage. In this experiment, the lack of the CTD was the only biochemical change.

5) In the Sec31ΔCTD section, the authors should comment on why ΔCTD is so deleterious to oligomer organization in yeast when cages form so abundantly in preparations of human Sec13/31 ΔC (Paraan et al 2018).

We have added a comment to address this. “Interestingly, human Sec31 proteins lacking the CTD assemble in cages, indicating that either the vertex is more stable for human proteins and sufficient for assembly, or that the CTD is important in the context of membrane budding but not for cage formation in high salt conditions.”

6) The data is good for the existence of the "extra rods", but significance and importance of them is not clear. How can these extra densities be distinguished from packing artifacts due to imperfections in the helical symmetry.

Please also see our response to point 3 from reviewer 1. Regarding the specific concern that artefacts might be a consequence of imperfection in the helical symmetry, we would argue such imperfections are indeed expected in physiological conditions, and to a much higher extent. For this reason interactions seen in the context of helical imperfections are likely to be relevant. In fact, in normal GTP hydrolysis conditions, we expect long tubes would not be able to form, and the outer coat to be present on a wide range of continuously changing membrane curvatures. We think that the ability of the coat to form many interactions when the symmetry is imperfect might be exactly what confers the coat its flexibility and adaptability.

7) Figure 5 is very hard to interpret and should be redone. Panels B and C are particularly hard to interpret.

We have made a new figure where we think clarity is improved.

8) The features present in Sec23/24 structure do not reflect the reported resolution of 4.7 Å. It seems that the resolution is overestimated.

We report an average resolution of 4.6 Å. In most of our map we can clearly distinguish beta strands, follow the twist of alpha helices and see bulky side chains. These features typically become visible at 4.5-5A resolution. We agree that some areas are worse than 4.6 Å, as typically expected for such a flexible assembly, but we believe that the average resolution value reported is accurate. We obtained the same resolution estimate using different software including relion, phenix and dynamo, so that is really the best value we can provide. To further convince ourselves that we have the resolution we claim, we sampled EM maps from the EMDB with the same stated resolution (we just took the 7 most recent ones which had an associated atomic model), and visualised their features at arbitrary positions. For both beta strands and alpha helices, we do not feel our map looks any worse than the others we have examined. We include a figure here.

9) Lines 315/316 - "We have combined cryo-tomography with biochemical and genetic assays to obtain a complete picture of the assembled COPII coat at unprecedented resolution (Fig. 7)"

10) Figure 7. is a schematic model/picture the authors should reference a different figure or rephrase the sentence.

We now refer to Fig 7 in a more appropriate place.

Reviewer #3:

The manuscript by Hutchings et al. describes several previously uncharacterised molecular interactions in the coats of COP-II vesicles by using a reconstituted coats of yeast COPI-II. They have improved the resolution of the inner coat to 4.7A by tomography and subtomogram averaging, revealing detailed interactions, including those made by the so-called L-loop not observed before. Analysis of the outer layer also led to new interesting discoveries. The sec 31 CTD was assigned in the map by comparing the WT and deletion mutant STA-generated density maps. It seems to stabilise the COP-II coats and further evidence from yeast deletion mutants and microsome budding reconstitution experiments suggests that this stabilisation is required in vitro. Furthermore, COP-II rods that cover the membrane tubules in right-handed manner revealed sometimes an extra rod, which is not part of the canonical lattice, bound to them. The binding mode of these extra rods (which I refer to here a Y-shape) is different from the canonical two-fold symmetric vertex (X-shape). When the same binding mode is utilized on both sides of the extra rod (Y-Y) the rod seems to simply insert in the canonical lattice. However, when the Y-binding mode is utilized on one side of the rod and the X-binding mode on the other side, this leads to bridging different lattices together. This potentially contributes to increased flexibility in the outer coat, which maybe be required to adopt different membrane curvatures and shapes with different cargos. These observations build a picture where stabilising elements in both COP-II layers contribute to functional cargo transport. The paper makes significant novel findings that are described well. Technically the paper is excellent and the figures nicely support the text. I have only minor suggestions that I think would improve the text and figure.

We thank the reviewer for helpful suggestions which we agree improve the manuscript.

Minor Comments:

L 108: "We collected .... tomograms". While the meaning is clear to a specialist, this may sound somewhat odd to a generic reader. Perhaps you could say "We acquired cryo-EM data of COP-II induced tubules as tilt series that were subsequently used to reconstruct 3D tomograms of the tubules."

We have changed this as suggested

L 114: "we developed an unbiased, localisation-based approach". What is the part that was developed here? It seems that the inner layer particle coordinates where simply shifted to get starting points in the outer layer. Developing an approach sounds more substantial than this. Also, it's unclear what is unbiased about this approach. The whole point is that it's biased to certain regions (which is a good thing as it incorporates prior knowledge on the location of the structures).

We have modified the sentence to “To target the sparser outer coat lattice for STA, we used the refined coordinates of the inner coat to locate the outer coat tetrameric vertices”, and explain the approach in detail in the methods.

L 124: "The outer coat vertex was refined to a resolution of approximately ~12 A, revealing unprecedented detail of the molecular interactions between Sec31 molecules (Supplementary Fig 2A)". The map alone does not reveal molecular interactions; the main understanding comes from fitting of X-ray structures to the low-resolution map. Also "unprecedented detail" itself is somewhat problematic as the map of Noble et al (2013) of the Sec31 vertex is also at nominal resolution of 12 A. Furthermore, Supplementary Fig 2A does not reveal this "unprecedented detail", it shows the resolution estimation by FSC. To clarify, these points you could say: "Fitting of the Sec31 atomic model to our reconstruction vertex at 12-A resolution (Supplementary Fig 2A) revealed the molecular interactions between different copies of Sec31 in the membrane-assembled coat.

We have changed the sentence as suggested.

L 150: Can the authors exclude the possibility that the difference is due to differences in data processing? E.g. how the maps amplitudes have been adjusted?

Yes, we can exclude this scenario by measuring distances between vertices in the right and left handed direction. These measurements are only compatible with our vertex arrangement, and cannot be explained by the big deviation from 4-fold symmetry seen in the membrane-less cage vertices.

L 172: "that wrap tubules either in a left- or right-handed manner". Don't they do always both on each tubule? Now this sentence could be interpreted to mean that some tubules have a left-handed coat and some a right-handed coat.

We have changed this sentence to clarify. “Outer coat vertices are connected by Sec13-31 rods that wrap tubules both in a left- and right-handed manner.”

L276: "The difference map" hasn't been introduced earlier but is referred to here as if it has been.

We now introduce the difference map.

L299: Can "Secondary structure predictions" denote a protein region "highly prone to protein binding"?

Yes, this is done through DISOPRED3, a feature include in the PSIPRED server we used for our predictions. The reference is: Jones D.T., Cozzetto D. DISOPRED3: precise disordered region predictions with annotated protein-binding activity Bioinformatics. 2015; 31:857–863. We have now added this reference to the manuscript.

L316: It's true that the detail in the map of the inner coat is unprecedented and the model presented in Figure 7 is partially based on that. But here "unprecedented resolution" sounds strange as this sentence refers to a schematic model and not a map.

We have changed this by moving the reference to Fig 7 to a more appropriate place

L325: "have 'compacted' during evolution" -> remove. It's enough to say it's more compact in humans and less compact in yeast as there could have been different adaptations in different organisms at this interface.

We have changed as requested. See also our response to reviewer 1, point 1.

L327: What's exactly meant by "sequence diversity or variability at this density".

We have now clarified: “Since multiple charge clusters in yeast Sec31 may contribute to this interaction interface (Stancheva et al., 2020), the low resolution could be explained by the fact that the density is an average of different sequences.”

L606-607: The description of this custom data processing approach is difficult to follow. Why is in-plane flip needed and how is it used here?

Initially particles are picked ignoring tube directionality (as this cannot be assessed easily from the tomograms due to the pseudo-twofold symmetry of the Sec23/24/Sar1 trimer). So the in plane rotation of inner coat subunit could be near 0 or 180°. For each tube, both angles are sampled (in-plane flip). Most tubes result in the majority of particles being assigned one of the two orientations (which is then assumed as the tube directionality). Particles that do not conform are removed, and rare tubes where directionality cannot be determined are also removed. We have re-written the description to clarify these points: “Initial alignments were conducted on a tube-by-tube basis using the Dynamo in-plane flip setting to search in-plane rotation angles 180° apart. This allowed to assign directionality to each tube, and particles that were not conforming to it were discarded by using the Dynamo dtgrep_direction command in custom MATLAB scripts”

L627: "Z" here refers to the coordinate system of aligned particles not that of the original tomogram. Perhaps just say "shifted 8 pixels further away from the membrane".

Changed as requested.

L642-643: How can the "left-handed" and "right-handed" rods be separated here? These terms refer to the long-range organisation of the rods in the lattice it's not clear how they were separated in the early alignments.

They are separated by picking only one subset using the dynamo sub-boxing feature. This extracts boxes from the tomogram which are in set positions and orientation relative to the average of previously aligned subtomograms. From the average vertex structure, we sub-box rods at 4 different positions that correspond to the centre of the rods, and the 2-fold symmetric pairs are combined into the same dataset. We have clarified this in the text: “The refined positions of vertices were used to extract two distinct datasets of left and right-handed rods respectively using the dynamo sub-boxing feature.”

Figure 2B. It's difficult to see the difference between dark and light pink colours.

We have changed colours to enhance the difference.

Figure 3C. These panels report the relative frequency of neighbouring vertices at each position; "intensity" does not seem to be the right measure for this. You could say that the colour bar indicates the "relative frequency of neighbouring vertices at each position" and add detail how the values were scaled between 0 and 1. The same applies to SFigure 1E.

Changed as requested.

Figure 4. The COP-II rods themselves are relatively straight, and they are not left-handed or right-handed. Here, more accurate would be "architecture of COPII rods organised in a left-handed manner". (In the text the authors may of course define and then use this shorter expression if they so wish.) Panel 4B top panel could have the title "left-handed" and the lower panel should have the title "right-handed" (for consistency and clarity).

We have now defined left- and right-handed rods in the text, and have changed the figure and panel titles as requested.

Author Response

Reviewer #1:

This paper addresses the very interesting topic of genome evolution in asexual animals. While the topic and questions are of interest, and I applaud the general goal of a large-scale comparative approach to the questions, there are limitations in the data analyzed. Most importantly, as the authors raise numerous times in the paper, questions about genome evolution following transitions to asexuality inherently require lineage-specific controls, i.e. paired sexual species to compare with the asexual lineages. Yet such data are currently lacking for most of the taxa examined, leaving a major gap in the ability to draw important conclusions here. I also do not think the main positive results, such as the role of hybridization and ploidy on the retention and amount of heterozygosity, are novel or surprising.

We agree with the reviewer that having the sexual outgroups would improve the interpretations; this is one of the points we make in our manuscript. Importantly however, all previous genome studies of asexual species focus on individual asexual lineages, generally without sexual species for comparison. Yet reported genome features have been interpreted as consequences of asexuality (e.g., Flot et al. 2013). By analysing and comparing these genomes, we can show that these features are in fact lineage-specific rather than general consequences of asexuality. Unexpectedly, we find that asexuals that are not of hybrid origin are largely homozygous, independently of the cellular mechanism underlying asexuality. This contrasts with the general view that cellular mechanisms such as central fusion (which facilitates heterozygosity retention between generation) promotes the evolutionary success of asexual lineages relative to mechanisms such as gamete duplication (which generate complete homozygosity) by delaying the expression of the recessive load. We also do not observe the expected relationship between cellular mechanism of asexuality and heterozygosity retention in species of hybrid origin. Thus we respectfully disagree that our results are not surprising. Reviewer #2 found our results “interesting” and a “potentially important contribution”, and reviewer #3 wrote that we “call into question the generality of the theoretical expectations, and suggest that the genomic impacts of asexuality may be more complicated than previously thought”.

We also make it very clear that some of the patterns we uncover (e.g. low TE loads in asexual species) cannot be clearly evaluated with asexuals alone. Our study emphasizes the importance of the fact that asexuality is a lineage-level trait and that comparative analyses using asexuals requires lineage-level replication in addition to comparisons to sexual species.

References

Flot, Jean-François, et al. "Genomic evidence for ameiotic evolution in the bdelloid rotifer Adineta vaga." Nature 500.7463 (2013): 453-457.

Reviewer #2:

[...] Major Issues and Questions:

1) The authors choose to refer to asexuality when describing thelytokous parthenogenesis. Asexuality is a very general term that can be confusing: fission, vegetative reproduction could also be considered asexuality. I suggest using parthenogenesis throughout the manuscript for the different animal clades studied here. Moreover, in thelytokous parthenogenesis meiosis can still occur to form the gametes, it is therefore not correct to write that "gamete production via meiosis... no longer take place" (lines 57-58). Fertilization by sperm indeed does not seem to take place (except during hybridogenesis, a special form of parthenogenesis).

We will clarify more explicitly what asexuality refers to in our manuscript. Notably our study does not include species that produce gametes which are fertilized (which is the case under hybridogenesis, which sensu stricto is not a form of parthenogenesis). Even though many forms of parthenogenesis do indeed involve meiosis (something we explain in much detail in box 2), there is no production of gametes.

2) The cellular mechanisms of asexuality in many asexual lineages are known through only a few, old cytological studies and could be inaccurate or incomplete (for example Triantaphyllou paper of 1981 of Meloidogyne nematodes or Hsu, 1956 for bdelloid rotifers). The authors should therefore mention in the introduction the lack of detailed and accurate cellular and genetic studies to describe the mode of reproduction because it may change the final conclusion.

For example, for bdelloid rotifers the literature is scarce. However the authors refer in Supp Table 1 to two articles that did not contain any cytological data on oogenesis in bdelloid rotifers to indicate that A. vaga and A. ricciae use apomixis as reproductive mode. Welch and Meselson studied the karyotypes of bdelloid rotifers, including A. vaga, and did not conclude anything about absence or presence of chromosome homology and therefore nothing can be said about their reproduction mode. In the article of Welch and Meselson the nuclear DNA content of bdelloid species is measured but without any link with the reproduction mode. The only paper referring to apomixis in bdelloids is from Hsu (1956) but it is old and new cytological data with modern technology should be obtained.

We will correct the rotifer citations and thank the reviewer for picking up the error. We agree that there are uncertainties in some cytological studies, but the same is true for genomic studies (which is why we base our analyses as much as possible on raw reads rather than assemblies because the latter may be incorrect). We in fact excluded cytological studies where the findings could not be corroborated. For example, we discarded the evidence for meiosis and diploidy by Handoo at al. 2004 for its incompatibility with genomic data because this study does not provide any verifiable evidence (there are no data or images, only descriptions of observations). We provide all the references in the supplementary material concerning the cytological evidence used.

3) In the section on Heterozygosity, the authors compute heterozygosity from kmer spectra analysis from reads to "avoid biases from variable genome assembly qualities" (page 16). But such kmer analysis can be biased by the quality and coverage of sequencing reads. While such analyses are a legitimate tool for heterozygosity measurements, this argument (the bias of genome quality) is not convincing and the authors should describe the potential limits of using kmer spectra analyses.

We excluded all the samples with unsuitable quality of data (e.g. one tardigrade species with excessive contamination or the water flea samples for insufficient coverage), and T. Rhyker Ranallo Benavidez, the author of the method we used, collaborated with us on the heterozygosity analyzes. However, we will clarify the limitations of the method for species with extremely low or high heterozygosity (see also comment 5 of this reviewer).

4) The authors state that heterozygosity levels “should decay over time for most forms of meiotic asexuality". This is incorrect, as this is not expected with "central fusion" or with "central fusion automixis equivalent" where there is no cytokinesis at meiosis I.

Our statement is correct. Note that we say “most” and not “all” because certain forms of endoduplication in F1 hybrids result in the maintenance of heterozygosity. Central fusion is expected to fully retain heterozygosity only if recombination is completely suppressed (see for example Suomalainen et al. 1987 or Engelstädter 2017).

5) I do not fully agree with the authors’ statement that: "In spite of the prediction that the cellular mechanism of asexuality should affect heterozygosity, it appears to have no detectable effect on heterozygosity levels once we control for the effect of hybrid origins (Figure 2)." (page 17)

The scaling on Figure 2 is emphasizing high values, while low values are not clearly separated. By zooming in on the smaller heterozygosity % values we may observe a bigger difference between the "asexuality mechanisms". I do not see how asexuality mechanism was controlled for, and if you look closely at intra group heterozygosity, variability is sometimes high.

It is expected that hybrid origin leads to higher heterozygosity levels but saying that asexuality mechanism is not important is surprising: on Figure 2 the orange (central fusion) is always higher than yellow (gamete duplication).

As we explain in detail in the text, the three comparatively high heterozygosity values under spontaneous origins of asexuality (“orange” points in the bottom left corner of the figure) are found in an only 40-year old clone of the Cape bee. Among species of hybrid origin, we see no correlation between asexuality mechanism and heterozygosity. These observations suggest that the asexuality mechanism may have an impact on genome-wide heterozygosity in recent incipient asexual lineages, but not in established asexual lineages.

Also, the variability found within rotifers could be an argument against a strong importance of asexuality origin on heterozygosity levels: the four bdelloid species likely share the same origin but their allelic heterozygosity levels appears to range from almost 0 to almost 6% (Fig 2 and 3, however the heterozygosity data on Rotaria should be confirmed, see below).

We prefer not using the data from rotifers for making such arguments, given the large uncertainty with respect to genome features in this group (including the possibility of octoploidy in some species which we describe in the supplemental information). One could even argue that the highly variable genome structure among rotifer species could indicate repeated transitions to asexuality and/or different hybridization events, but the available genome data would make all these arguments highly speculative.

The authors’ main idea (i.e. asexuality origin is key) seems mostly true when using homoeolog heterozygosity and/or composite heterozygosity which is not what most readers will usually think as "heterozygosity". This should be made clear by the authors mostly because this kind of heterozygosity does not necessarily undergo the same mechanism as the one described in Box 2 for allelic heterozygosity. If homoeolog heterozygosity is sometimes not distinguishable from allelic heterozygosity, then it would be nice to have another box showing the mechanisms and evolution pattern for such cases (like a true tetraploid, in which all copies exist).

The heterozygosity between homoeologs is always high in this study while it appears low between alleles, but since the heterozygosity between homeologs can only be measured when there is a hybrid origin, the only heterozygosity that can be compared between ALL the asexual groups is the one between alleles.

By definition, homoeologs have diverged between species, while alleles have diverged within species. So indeed divergence between homoeologs will generally exceed divergence between alleles. We will consider adding expected patterns in perfect tetraploid species for Box 2.

Both in the results and the conclusion the authors should not over interpret the results on heterozygosity. The variation in allelic heterozygosity could be small (although not in all asexuals studied) also due to the age of the asexual lineages. This is not mentioned here in the result/discussion section..

We explain in section Overview of species and genomes studied that age effects are important but that we do not consider them quantitatively because age estimates are not available for the majority of asexual species in our paper.

6) Regarding the section on Heterozygosity structure in polyploids

There is inconsistency in many of the numbers. For example, A. vaga heterozygosity is estimated at 1.42% in Figure 1, but then appears to show up around 2% in Figure 2, and then becomes 2.4% on page 20. It is unclear is this is an error or the result of different methods.

It is also unclear how homologs were distinguished from homeologs. How are 21 bp k-mers considered homologous? In the method section. the authors describe extracting unique k-mer pairs differing by one SNP, so does this mean that no more than one SNP was allowed to define heterozygous homologous regions? Does this mean that homologues (and certainly homoeologs) differing by more than 5% would not be retrieved by this method. If so, then It is not surprising that for A.vaga is classified as a diploid.

Figure 1 a presents the values reported in the original genome studies, not our results. This is explained in the corresponding figure legend. Hence, 1.42 is the value reported by Flot at al. 2013. 2.4 is the value we measure and it is consistent in Figures 2 and 3.

We used k-mer pairs differing by one SNP to estimate ploidy (smudgeplot). The heterozygosity estimates were estimated from kmer spectra (GenomeScope 2.0). The kmers that are found in 1n must be heterozygous between homologs, as the homoeolog heterozygosity would produce 2n kmers, We used the kmer approach to estimate heterozygosity in all other cases than homoeologs of rotifers, which were directly derived from the assemblies. We explain this in the legend to Figure 3, but we will add the information also to the Methods section for clarification.

The result for A. ricciae is surprising and I am still not convinced by the octoploid hypothesis. In Fig S2. there is a first peak at 71x coverage that still could be mostly contaminants. It would be helpful to check the GC distribution of k-mers in the first haploid peak of A. ricciae to check whether there are contaminants. The karyotypes of 12 chromosomes indeed do not fit the octoploid hypothesis. I am also surprised by the 5.5% divergence calculated for A. ricciae, this value should be checked when eliminating potential contaminants (if any). In general, these kind of ambiguities will not be resolved without long-read sequencing technology to improve the genome assemblies of asexual lineages.

We understand the scepticism of the reviewer regarding the octoploidy hypothesis, but it is important to note that we clearly present it as a possible explanation for the data that needs to be corroborated, i.e., we state that the data are better consistent with octo- than tetraploidy. Contamination seems quite unlikely, as the 71.1x peak represents nearly exactly half the coverage of the otherwise haploid peak (142x). Furthermore, the Smudgeplot analysis shows that some of the kmers from the 71x peak pair with genomic kmers of the main peaks. We also performed KAT analysis (not presented in the manuscript) showing that these kmers are also represented in the decontaminated assembly. We will add this clarification regarding possible contamination to the supplementary materials.

7) Regarding the section on palindromes and gene conversion

The authors screened all the published genomes for palindromes, including small blocks, to provide a more robust unbiased view. However, the result will be unbiased and robust if all the genomes compared were assembled using the same sequencing data (quality, coverage) and assembly program. While palindromes appear not to play a major role in the genome evolution of parthenogenetic animals since only few palindromes were detected among all lineages, mitotic (and meiotic) gene conversion is likely to take place in parthenogens and should indeed be studied among all the clades.

We agree with the reviewer that gene conversion might be one of the key aspects of asexual genome evolution. Our study merely pointed out that genomes of asexual animals do not show organisation in palindromes, indicating that palindromes might not be of general importance in asexual genome evolution. Note also that we clearly point out that these analyses are biased by the quality of the available genome assemblies.

8) Regarding the section on transposable elements

The authors are aware that the approach used may underestimate the TEs present in low copy numbers, therefore the comparison might underestimate the TE numbers in certain asexual groups.

Yes. We clearly explain this limitation in the manuscript. The currently available alternatives are based on assembled genomes, so the results are biased by the quality of the assemblies (and similarities to TEs in public databases) and our aim was to broadly compare genomes in the absence of assembly-generated biases.

9) Regarding the section on horizontal gene transfer. For the HGTc analysis, annotated genes were compared to the UniRef90 database to identify non-metazoan genes and HGT candidates were confirmed if they were on a scaffold containing at least one gene of metazoan origin. While this method is indeed interesting, it is also biased by the annotation quality and the length of the scaffolds which vary strongly between studies.

Yes, this is true and we explain many limitations in the supplemental information, but re-assembling and re-annotating all these genomes would be beyond reasonable computational possibilities.

10) Regarding the use of GenomeScope2.0

When homologues are very divergent (as observed in bdelloid rotifers) GenomeScope probably considers these distinct haplotypes as errors, making it difficult to model the haploid genome size and giving a high peak of errors in the GenomeScope profile. Moreover, due to the very divergent copies in A. vaga, GenomeScope indeed provides a diploid genome (instead of tetraploid).

For A. vaga, the heterozygosity estimated par GenomeScope2.0. on our new sequencing dataset is 2% (as shown in this paper). This % corresponds to the heterozygosity between k-mers but does not provide any information on the heterogeneity in heterozygosity measurements along the genome. A limitation of GenomeScope2.0. (which the authors should mention here) is that it is assuming that the entire genome is following the same theoretical k-mer distribution.

The model of estimating genome wide heterozygosity indeed assumes a random distribution of heterozygous loci and indeed is unable to estimate divergence over a certain threshold, which is the reason why we used genome assemblies for the estimation of divergence of homoeologs. Regarding estimates in all other genomes, the assumptions are unlikely to fundamentally change the output of the analysis. GenomeScope2 is described in detail in a recent paper (Ranallo-Benavidez et al. 2019), where the assumption that heterozygosity rates are constant across the genome is explicitly mentioned.

References

Engelstädter, Jan. "Asexual but not clonal: evolutionary processes in automictic populations." Genetics 206.2 (2017): 993-1009.

Flot, Jean-François, et al. "Genomic evidence for ameiotic evolution in the bdelloid rotifer Adineta vaga." Nature 500.7463 (2013): 453-457.

Handoo, Z. A., et al. "Morphological, molecular, and differential-host characterization of Meloidogyne floridensis n. sp.(Nematoda: Meloidogynidae), a root-knot nematode parasitizing peach in Florida." Journal of nematology 36.1 (2004): 20.

Suomalainen, Esko, Anssi Saura, and Juhani Lokki. Cytology and evolution in parthenogenesis. CRC Press, 1987.

Ranallo-Benavidez, Timothy Rhyker, Kamil S. Jaron, and Michael C. Schatz. "GenomeScope 2.0 and Smudgeplots: Reference-free profiling of polyploid genomes." BioRxiv (2019): 747568. 

Reviewer #3:

Jaron and collaborators provide a large-scale comparative work on the genomic impact of asexuality in animals. By analysing 26 published genomes with a unique bioinformatic pipeline, they conclude that none of the expected features due to the transition to asexuality is replicated across a majority of the species. Their findings call into question the generality of the theoretical expectations, and suggest that the genomic impacts of asexuality may be more complicated than previously thought.

The major strengths of this work is (i) the comparison among various modes and origins of asexuality across 18 independent transitions; and (ii) the development of a bioinformatic pipeline directly based on raw reads, which limits the biases associated with genome assembly. Moreover, I would like to acknowledge the effort made by the authors to provide on public servers detailed methods which allow the analyses to be reproduced. That being said, I also have a series of concerns, listed below:

We thank this reviewer for the relevant comments and for providing many constructive suggestions in the points below. We will take them into account for our final version of the manuscript.

1) Theoretical expectations

As far as I understand, the aim of this work is to test whether 4 classical predictions associated with the transition to asexuality and 5 additional features observed in individual asexual lineages hold at a large phylogenetic scale. However, I think that these predictions are poorly presented, and so they may be hardly understood by non-expert readers. Some of them are briefly mentioned in a descriptive way in the Introduction (L56 - 61), and with a little more details in the Boxes 1 and 2. However, the evolutive reasons why one should expect these features to occur (and under which assumptions) is not clearly stated anywhere in the Introduction (but only briefly in the Results & Discussion). I think it is important that the authors provide clear-cut quantitative expectations for each genomic feature analysed and under each asexuality origin and mode (Box 1 and 2). Also highlighting the assumptions behind these expectations will help for a better interpretation of the observed patterns.

We will clarify the expectations for non expert readers.

2) Mutation accumulation & positive selection

A subtlety which is not sufficiently emphasized to my mind is that the different modes of asexuality encompass reproduction with or without recombination (Box 2), which can lead to very different genetic outcomes. For example, it has been shown that the Muller's ratchet (the accumulation of deleterious mutations in asexual populations) can be stopped by small amounts of recombination in large-sized populations (Charlesworth et al. 1993; 10.1017/S0016672300031086). Similarly a new recessive beneficial mutation can only segregate at a heterozygous state in a clonal lineage (unless a second mutation hits the same locus); whereas in the presence of recombination, these mutations will rapidly fix in the population by the formation of homozygous mutants (Haldane's Sieve, Haldane 1927; 10.1017/S0305004100015644). Therefore, depending on whether recombination occurs or not during asexual reproduction, the expectations may be quite different; and so they could deviate from the "classical predictions". In this regard, I would like to see the authors adjust their conclusions. Moreover, it is also not very clear whether the species analysed here are 100% asexuals or if they sometimes go through transitory sexual phases, which could reset some of the genomic effects of asexuality.

Yes, the predictions regarding the efficiency of selection are indeed influenced by cellular modes of asexuality. Adding some details or at least a good reference would certainly increase the readability of the section. We thank the reviewer for this suggestion.

3) Transposable elements

I found the predictions regarding the amount of TEs expected under asexuality quite ambiguous. From one side, TEs are expected not to spread because they cannot colonize new genomes (Hickey 1982); but on the other side TEs can be viewed as any deleterious mutation that will accumulate in asexual genome due to the Muller's ratchet. The argument provided by the authors to justify the expectation of low TE load in asexual lineages is that "Only asexual lineages without active TEs, or with efficient TE suppression mechanisms, would be able to persist over evolutionary timescales". But this argument should then equally be applied to any other type of deleterious mutations, and so we won't be able to see Muller's ratchet in the first place. Therefore, not observing the expected pattern for TEs in the genomic data is not so surprising as the expectation itself does not seem to be very robust. I would like the authors to better acknowledge this issue, which actually goes into their general idea that the genomic consequences of asexuality are not so simple.

Indeed, the survivorship bias should affect all genomic features. Nothing that is incompatible with the viability of the species will ever be observed in nature. Perhaps the difference between Muller’s ratchet and the dynamics of accumulation of transposable elements (TEs) is that TEs are expected to either propagate very fast or not at all (Dolgin and Charlesworth 2006), while the effects of Muller’s ratchet are expected to vary among different populations and cellular mechanisms of asexuality. We will rephrase the text to better reflect the complexity of the predicted consequences of TE dynamics.

4) Heterozygosity

Due to the absence of recombination, asexual populations are expected to maintain a high level of diversity at each single locus (heterozygosity), but a low number of different haplotypes. However, as presented by the authors in the Box 2, there are different modes of parthenogenesis with different outcomes regarding heterozygosity: (1) preservation at all loci; (2) reduction or loss at all loci; (3) reduction depending on the chromosomal position relative to the centromere (distal or proximal). Therefore, the authors could benefit from their genome-based dataset to explore in more detail the distribution of heterozygosity along the chromosomes, and further test whether it fits with the above predictions. If the differing quality of the genome assemblies is an issue, the authors could at least provide the variance of the heterozygosity across the genome. The mode #3 (i.e. central fusions and terminal fusions) would be particularly interesting as one would then be able to compare, within the same genome, regions with large excess vs. deficit of heterozygosity and assess their evolutive impacts.

Moreover, the authors should put more emphasis on the fact that using a single genome per species is a limitation to test the subtle effects of asexuality on heterozygosity (and also on "mutation accumulation & positive selection"). These effects are better detected using population-based methods (i.e. with many individuals, but not necessarily many loci). For example, the FIS value of a given locus is negative when its heterozygosity is higher than expected under random mating, and positive when the reverse is true (Wright 1951; 10.1111/j.1469-1809.1949.tb02451.x).

We agree with the reviewer that the analysis of the distribution of heterozygosity along the chromosomes would be very interesting. However, the necessary data is available only for the Cape honey bee, and its analysis has been published by Smith et al. 2018. Calculating the probability distribution of heterozygosities would be possible, but it would require SNP calling for each of the datasets. Such an analysis would be computationally intensive and prone to biases by the quality of the genome assemblies.

5) Absence of sexual lineages

A second limit of this work is the absence of sexual lineages to use as references in order to control for lineage-specific effects. I do not agree with the authors when they say that "the theoretical predictions pertaining to mutation accumulation, positive selection, gene family expansions, and gene loss are always relative to sexual species [...] and cannot be independently quantified in asexuals." I think that this is true for all the genomic features analysed, because the transition to asexuality is going to affect the genome of asexual lineages relative to their sexual ancestors. This is actually acknowledged at the end of the Conclusion by the authors.

To give an example, the authors say that "Species with an intraspecific origin of asexuality show low heterozygosity levels (0.03% - 0.83%), while all of the asexual species with a known hybrid origin display high heterozygosity levels (1.73% - 8.5%)". Interpreting these low vs. high heterozygosity values is difficult without having sexual references, because the level of genetic diversity is also heavily influenced by the long term life history strategies of each species (e.g. Romiguier et al. 2014; 10.1038/nature13685).

I understand that the genome of related sexual species are not available, which precludes direct comparisons with the asexual species. However, I think that the results could be strengthened if the authors provided for each genomic feature that they tested some estimates from related sexual species. Actually, they partially do so along the Result & Discussion section for the palindromes, transposable elements and horizontal gene transfers. I think that these expectations for sexual species (and others) could be added to Table 1 to facilitate the comparisons.

Our statement "the theoretical predictions pertaining to mutation accumulation, positive selection, gene family expansions, and gene loss are always relative to sexual species [...] and cannot be independently quantified in asexuals." specifically refers to methodology: analyses to address these predictions require orthologs between sexual and asexual species. We fully agree that in addition to methodological constraints, comparisons to sexual species are also conceptually relevant - which is in fact one of the major points of our paper. We will clarify these points.

6) Regarding statistics, I acknowledge that the number of species analysed is relatively low (n=26), which may preclude getting any significant results if the effects are weak. However, the authors should then clearly state in the text (and not only in the reporting form) that their analyses are descriptive. Also, their position regarding this issue is not entirely clear as they still performed a statistical test for the effect of asexuality mode / origin on TE load (Figure 2 - supplement 1). Therefore, I would like to see the same statistical test performed on heterozygosity (Figure 2).

We will unify the sections and add an appropriate test everywhere where suited.

7) As you used 31 individuals from 26 asexual species, I was wondering whether you make profit of the multi-sample species. For example, were the kmer-based analyses congruent between individuals of the same species?

Unfortunately, some of the 31 individuals do not have publicly available reads (some of the root-knot nematode datasets are missing), others do not have sufficient quality (the coverage for some water flea samples is very low). Our analyses were consistent for the few cases where we have multiple datasets available.

References

Dolgin, Elie S., and Brian Charlesworth. "The fate of transposable elements in asexual populations." Genetics 174.2 (2006): 817-827.

Smith, Nicholas MA, et al. "Strikingly high levels of heterozygosity despite 20 years of inbreeding in a clonal honey bee." Journal of evolutionary biology 32.2 (2019): 144-152.

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Referee #2

Evidence, reproducibility and clarity

This study by Louka et al., investigates the function of Cep104, a protein associated with Joubert syndrome, in Xenopus. Several aspects are studied at different scales. Loss of function of this protein suggests a role in neural tube closure, apical constriction, and HH signaling. Moving on in the study, the authors investigate the localization of Cep104 in the primary cilia of the neural tube before focusing on its localization in multiciliated cells. They then look at the consequences of loss of function on motile cilia and conclude that it plays a role in the length of the distal segment. They then show an association of Cep104 with cytoplasmic microtubules in non-multiciliated cells of the Xenopus epidermis. They then analyze the function of Cep104 on these microtubules and show that loss of Cep104 function increases the speed of EB1 comets. They then looked at the impact of loss of function on microtubule stability and finally the impact of gain of function. Finally, they returned to the multiciliated cells and described an intercalation defect that correlated with decreases in acetylated tubulin. I think that certain controls are missing and that the choice of illustrations should be reconsidered (better quality, appropriate zoom). In terms of form, the text is not easy to read and the manuscript would benefit from reformatting to highlight the logical links between the different experiences and avoid a catalog-like effect. I would advise the authors to revise their introduction to make it less disjointed and guide readers toward the questions addressed by the manuscript.

Below are specific comments and remarks:

Figure 1:

Why the conclusion is a "delay" in neural tube closure? At what stage is this analyzed? Is there a recovery of NT closure at later stage? A: I would suggest to provide control picture of non-injected and tracer only injected embryos. B: Statistics are missing on the graph D: mention what was injected instead of "+ rescue". Close up picture would allow a better appreciation of the differences in surface area.

Figure S1:

To illustrate the claim that cilia are not affected, it would be good to show injection of tracer alone and compare to tracer + morpholino. Also, to provide a measure of the cilia size.

Figure 2:

Please provide pictures to illustrate graph D.

Figure 5:

"Interestingly, most of the nocodazole-resistant stable microtubules were positive for Cep104 (Figure 5C, arrows). " - The variation in density of Cep104-GFP signal is not visible on the pictures provided in C. I would suggest to show higher magnifications. Also, in the DMSO treated picture the Cep104GFP signal looks really different when compared to Cep104-GFP signal shown in B. Arrows should be reported on all channels. However, it not clear what we should see with this arrows. 5C: it seems that in nocodazole treated condition the Cep104-GFP is at the cilia base in MCCs which is different from the DMSO control condition. The basal body signal was not seen in the figure 3A which analyze the localization of Cep104-GFP in MCCs. Why not comment on this? Is it a phenotype on MCCs ? Figure 6: Intriguingly, morphant non-MCCs have significantly more mean β-tubulin signal compared to control non-MCCs in embryos treated with DMSO (Figure 6C). - impossible to appreciate on the figures. Please specify on the figure what is considered as a morphant non-MCC versus a control non-MCC. The membrane-cherry positive cells (supposedly morphant? it has to be clarified show very heterogenous tubulin expression)

If the point here is to show that microtubules are more sensitive to nocodazole in morphant cells as compared to control. I would suggest to show all conditions on a same graph. At least annotate more the grap for a self-explanatory figure (DMSO , Nocodazole). Figure 7: Statistics are missing on Graph B Comment on the text: "Cep104 signal shows the characteristic two dot pattern in motile cilia (Figure 3A) that was also observed in a recent study using Xenopus Cep10465 and in the cilia of Tetrahymena50. This is in agreement with a recent study showing the characteristic two dot pattern for Xenopus Cep104 as well66 " - ref 65 and 66b are the same (Hong et al., preprint)

"This data suggests that downregulation of CEP104 affects the stability of cytoplasmic microtubules." - I would suggest a more precise conclusion by stating how is it affected? More stable? Less stable? Important for the follow-up demonstration.

Movies:

Please annotate properly movie 2 and 3 so the reader can know what he/she is looking.

Referees cross-commenting

Similar feeling that reviews are consistent

Significance

This study investigates the role of the proprotein Cep104 in Xenopus. Cep104 is a protein associated with Joubert syndrome, whose role in primary cilia has been extensively documented. While its localization at the tip of motile cilia has also been reported, this study provides functional evidence for the role of Cep104 in motile cilia. In addition, the study looks at the role of Cep104 on non-cilial microtubules, which is the original aspect of the paper and may ultimately lead to a better understanding of Joubert syndrome. However, I believe that the evidence provided (controls, illustrations) needs to be improved. This paper will be of interest to a specialized audience with an interest in proteins associated with cilia and microtubules.

I am a cell biologist specialized in the study of multiciliated cells using advanced imaging methods and Xenopus and mice as models. I believe my expertise was a perfect match for this manuscript.

Author Response:

Reviewer #1 (Public Review):

1. There was little comment on the strategy/mechanism that enabled subjects to readily attain Target I (MU 1 active alone), and then Target II (MU1 and MU2 active to the same relative degree). To accomplish this, it would seem that the peak firing rate of MU1 during pursuit of Target II could not exceed that during Target I despite an increased neural drive needed to recruit MU2. The most plausible explanation for this absence of additional rate coding in MU1 would be that associated with firing rate saturation (e.g., Fuglevand et al. (2015) Distinguishing intrinsic from extrinsic factors underlying firing rate saturation in human motor units. Journal of Neurophysiology 113, 1310-1322). It would be helpful if the authors might comment on whether firing rate saturation, or other mechanism, seemed to be at play that allowed subjects to attain both targets I and II.

To place the cursor inside TII, both MU1 and MU2 must discharge action potentials at their corresponding average discharge rate during 10% MVC (± 10% due to the target radius and neglecting the additional gain set manually in each direction). Therefore, subjects could simply exert a force of 10% MVC to reach TII and would successfully place the cursor inside TII. However, to get to TI, MU1 must discharge action potentials at the same rate as during TII hits (i.e. average discharge rate at 10% MVC) while keeping MU2 silent. Based on the performance analysis in Fig 3D, subjects had difficulties moving the cursor towards TI when the difference in recruitment threshold between MU1 and MU2 was small (≤ 1% MVC). In this case, the average discharge rate of MU1 during 10% MVC could not be reached without activating MU2. As could be expected, reaching towards TI became more successful when the difference in recruitment threshold between MU1 and MU2 was relatively large (≥3% MVC). In this case, subjects were able to let MU1 discharge action potentials at its average discharge rate at 10% MVC without triggering activation of MU2 (it seems the discharge rate of MU1 saturated before the onset of MU2). Such behaviour can be observed in Fig. 2A. MUs with a lower recruitment threshold saturate their discharge rate before the force reaches 10% MVC. We adapted the Discussion accordingly to describe this behaviour in more detail.

1. Figure 4 (and associated Figure 6) is nice, and the discovery of the strategy used by subjects to attain Target III is very interesting. One mechanism that might partially account for this behavior that was not directly addressed is the role inhibition may have played. The size principle also operates for inhibitory inputs. As such, small, low threshold motor neurons will tend to respond to a given amount of inhibitory synaptic current with a greater hyperpolarization than high threshold units. Consequently, once both units were recruited, subsequent gradual augmentation of synaptic inhibition (concurrent with excitation and broadly distributed) could have led to the situation where the low threshold unit was deactivated (because of the higher magnitude hyperpolarization), leaving MU2 discharging in isolation. This possibility might be discussed.

We agree with the reviewer’s comment that inhibition might have played a critical role in succeeding to reach TIII. Hence, we have added this concept to our discussion.

1. In a similar vein as for point 2 (above), the argument that PICs may have been the key mechanism enabling the attainment of target III, while reasonable, also seems a little hand wavy. The problem with the argument is that it depends on differential influences of PICs on motor neurons that are 1) low threshold, and 2) have similar recruitment thresholds. This seems somewhat unlikely given the broad influence of neuromodulatory inputs across populations of motor neurons.

We agree with the reviewer’s point and reasoning that a mixture of neuromodulation and inhibition likely introduced the variability in MU activity we observed in this study. This comment is addressed in the answer to comment 3.

Reviewer #2 (Public Review):

[...]

1. Some subjects seemed to hit TIII by repeatedly "pumping" the force up and down to increase the excitability of MU2 (this appears to happen in TIII trials 2-6 in Fig. 4 - c.f. p18 l30ff). It would be useful to see single-trial time series plots of MU1, MU2, and force for more example trials and sessions, to get a sense for the diversity of strategies subjects used. The authors might also consider providing additional analyses to test whether multiple "pumps" increased MU2 excitability, and if so, whether this increase was usually larger for MU2 than MU1. For example, they might plot the ratio of MU2 (and MU1) activation to force (or, better, the residual discharge rate after subtracting predicted discharge based on a nonlinear fit to the ramp data) over the course of the trial. Is there a reason to think, based on the data or previous work, that units with comparatively higher thresholds (out of a sample selected in the low range of <10% MVC) would have larger increases in excitability?


We added a supplementary figure (Supplement 4) that visualizes additional trials from different conditions and subjects for TIII-instructed trials and noted this in the text.

MU excitability might indeed be pronounced during repeated activations within a couple of seconds (see, for example, M. Gorassini, J. F. Yang, M. Siu, and D. J. Bennett, “Intrinsic Activation of Human Motoneurons: Reduction of Motor Unit Recruitment Thresholds by Repeated Contractions,” J. Neurophysiol., vol. 87, no. 4, pp. 1859–1866, 2002.). Such an effect, however, seems to be equally distributed to all active MUs. Moreover, we are not aware of any recent studies suggesting that MUs, within the narrow range of 0-10% MVC, may be excited differently by such a mechanism. Supplement 4C and D illustrate trials in which subjects performed multiple “pumps”. Visually, we could not find changes in the excitability specific to any of the two MUs nor that subjects explored repeated activation of MUs as a strategy to reach TIII. It seems subjects instead tried to find the precise force level which would allow them to keep MU2 active after the offset of MU1. We further discussed that PICs act very broadly on all MUs. The observed discharge patterns when successfully reaching TIII may likely be due to an interplay of broadly distributed neuromodulation and locally acting synaptic inhibition.

1. I am somewhat surprised that subjects were able to reach TIII at all when the de-recruitment threshold for MU1 was lower than the de-recruitment threshold for MU2. It would be useful to see (A) performance data, as in Fig. 3D or 5A, conditioned on the difference in de-recruitment thresholds, rather than recruitment thresholds, and (B) a scatterplot of the difference in de-recruitment vs the difference in recruitment thresholds for all pairs.


We agree that comparing the difference in de-recruitment threshold with the performance of reaching each target might provide valuable insights into the strategies used to perform the tasks. Hence, we added this comparison to Figure 4E at p. 16, l. 1. A scatterplot of the difference in de-recruitment threshold and the difference in recruitment threshold has been added to Supplement 3A. The Results section was modified in line with the above changes.

1. Using MU1 / MU2 rates to directly control cursor position makes sense for testing for independent control over the two MUs. However, one might imagine that there could exist a different decoding scheme (using more than two units, nonlinearities, delay coordinates, or control of velocity instead of position) that would allow subjects to generate smooth trajectories towards all three targets. Because the authors set their study in a BCI context, they may wish to comment on whether more complicated decoding schemes might be able to exploit single-unit EMG for BCI control or, alternatively, to argue that a single degree of freedom in input fundamentally limits the utility of such schemes.


This study aimed to assess whether humans can learn to decorrelate the activity between two MUs coming from the same functional MU pool during constraint isometric conditions. The biofeedback was chosen to encourage subjects to perform this non-intuitive and unnatural task. Transferring biofeedback on single MUs into an application, for example, BCI control, could include more advanced pre-processing steps. Not all subjects were able to navigate the cursor along both axes consistently (always hitting TI and TIII). However, the performance metric (Figure 4C) indicated that subjects became better over time in diverging from the diagonal and thus increased their moving range inside the 2D space for various combinations of MU pairs. Hence, a weighted linear combination of the activity of both MUs (for example, along the two principal components based on the cursor distribution) may enable subjects to navigate a cursor from one axis to another. Similarly, coadaptation methods or different types of biofeedback (auditory or haptic) may help subjects. Furthermore, using only two MUs to drive a cursor inside a 2-D space is prone to interference. Including multiple MUs in the control scheme may improve the performance even in the presence of noise. We have shown that the activation of a single MU pool exposed to a common drive does not necessarily obey rigid control. State-dependent flexible control due to variable intrinsic properties of single MUs may be exploited for specific applications, such as BCI. However, further research is necessary to understand the potentials and limits of such a control scheme.

1. The conclusions of the present work contrast somewhat with those of Marshall et al. (ref. 24), who claim (for shoulder and proximal arm muscles in the macaque) that (A) violations of the "common drive" hypothesis were relatively common when force profiles of different frequencies were compared, and that (B) microstimulation of different M1 sites could independently activate either MU in a pair at rest. Here, the authors provide a useful discussion of (A) on p19 l11ff, emphasizing that independent inputs and changes in intrinsic excitability cannot be conclusively distinguished once the MU has been recruited. They may wish to provide additional context for synthesizing their results with Marshall et al., including possible differences between upper / lower limb and proximal / distal muscles, task structure, and species.

The work by Marshall, Churchland and colleagues shows that when stimulating focally in specific sites in M1 single MUs can be activated, which may suggest a direct pathway from cortical neurons to single motor neurons within a pool. However, it remains to be shown if humans can learn to leverage such potential pathways or if the observations are limited to the artificially induced stimulus. The tibialis anterior receives a strong and direct cortical projection. Thus, we think that this muscle may be well suited to study whether subjects can explore such specific pathways to activate single MUs independently. However, it may very well be that the control of upper limbs show more flexibility than lower ones. However, we are not aware of any study that may provide evidence for a critical mismatch in the control of upper and lower limb MU pools. We have added this discussion to the manuscript.

Reviewer #3 (Public Review):

[...]

Even if the online decomposition of motor units were performed perfectly, the visual display provided to subject smooths the extracted motor unit discharge rates over a very wide time window: 1625 msec. This window is significantly larger than the differences in recruitment times in many of the motor unit pairs being used to control the interface. So while it's clear that the subjects are learning to perform the task successfully, it's not clear to me that subjects could have used the provided visual information to receive feedback about or learn to control motor unit recruitment, even if individuated control of motor unit recruitment by the nervous system is possible. I am therefore not convinced that these experiments were a fair test of subjects' ability to control the recruitment of individual motor units.

Regarding the validating of isolating motor units in the conditions analysed in this study, we have added a full new set of measurements with concomitant surface and intramuscular recordings during recruitment/derecruitment of motor units at variable recruitment speed. This provides a strong validation of the approach and of the accuracy of the online decomposition used in this study. Subjects received visual feedback on the activity of the selected MU pair, i.e. discharge behaviour of both MUs and the resulting cursor movement. This information was not clear from the initial submission and hence, we annotated the current version to clarify the biofeedback modalities. To further clarify the decoding of incoming MU1/MU2 discharge rates into cursor movement, we included Supplement 2. We also included a video that shows that the smoothing window on the cursor position does not affect the immediate cursor movement due to incoming spiking activity. For example, as shown in Supplement 2, for the initial offset of 0ms, the cursor starts moving along the axis corresponding to a sole activation of MU1 and immediately diverges from this axis when MU2 starts to discharge action potentials. We, therefore, think that the biofeedback provided to the subjects does allow exploration of single MU control.

Along similar lines, it seems likely to me that subjects are using some other strategy to learn the task, quite possibly one based on control of over overall force at the ankle and/or voluntary recruitment of other leg/foot muscles. Each of these variables will presumably be correlated with the activity of the recorded motor units and the movement of the cursor on the screen. Moreover, because these variables likely change on a similar (or slower) timescale than differences in motor units recruitment or derecruitment, it seems to me that using such strategies, which do not reflect or require individuated motor unit recruitment, is a highly effective way to successfully complete the task given the particular experimental setup.

In addition to being seated and restricted by an ankle dynamometer, subjects were instructed to only perform dorsiflexion of the ankle. Further, none of the subjects reported compensatory movements as a strategy to reach any of the targets. In addition, to be successfully utilised, such compensatory movements would need to influence various combinations of MUs tested in this study equally, even when they differ in size. Nevertheless, we acknowledge, as pointed out by the reviewer, that our setup has limitations. We only measured force in a single direction (i.e. ankle dorsiflexion) and did not track toe, hip or knee movements. Even though an instructor supervised leg movement throughout the experiment, it may be that very subtle and unknowingly compensatory movements have influenced the activity of the selected MUs. Hence, we updated the limitations section in the Discussion.

To summarize my above two points, it seems like the author's argument is that absence of evidence (subjects do not perform individuated MU recruitment in this particular task) constitutes evidence of absence (i.e. is evidence that individuated recruitment is not possible for the nervous system or for the control of brain-machine interfaces). Therefore given the above-described issues regarding real-time feedback provided to subjects in the paper it is not clear to me that any strong conclusions can be drawn about the nervous system's ability or inability to achieve individuated motor unit recruitment.

We hope that the above changes clarify the biofeedback modalities and their potential to provide subjects with the necessary information for exploring independent MU control. Our experiments aimed to investigate whether subjects can learn under constraint isometric conditions to decorrelate the activity between two MUs coming from the same functional pool. While it seemed that MU activity could be decorrelated, this almost exclusively happened (TIII-instructed trials) within a state-dependent framework, i.e. both MUs must be activated first before the lower threshold one is switched off. We did not observe flexible MU control based exclusively on a selective input to individual MUs (MU2 activated before MU1 during initial recruitment). That does not mean that such control is impossible. However, all successful control strategies that were voluntarily explored by the subjects to achieve flexible control were based on a common input and history-dependent activation of MUs. We have added these concepts to the discussion section.

Second, to support the claims based on their data the authors must explain their online spike-sorting method and provide evidence that it can successfully discriminate distinct motor unit onset/offset times at the low latency that would be required to test their claims. In the current manuscript, authors do not address this at all beyond referring to their recent IEEE paper (ref [25]). However, although that earlier paper is exciting and has many strengths (including simultaneous recordings from intramuscular and surface EMGs), the IEEE paper does not attempt to evaluate the performance metrics that are essential to the current project. For example, the key metric in ref 25 is "rate-of-agreement" (RoA), which measures differences in the total number of motor unit action potentials sorted from, for example, surface and intramuscular EMG. However, there is no evaluation of whether there is agreement in recruitment or de-recruitment times (the key variable in the present study) for motor units measured both from the surface and intramuscularly. This important technical point must be addressed if any conclusions are to be drawn from the present data.

We have taken this comment in high consideration, and we have performed a validation based on concomitant intramuscular and surface EMG decomposition in the exact experimental conditions of this study, including variations in the speed of recruitment and de-recruitment. This new validation fully supports the accuracy in of the methods used when detecting recruitment and de-recruitment of motor units.

My final concern is that the authors' key conclusion - that the nervous system cannot or does not control motor units in an individuated fashion - is based on the assumption that the robust differences in de-recruitment time that subjects display cannot be due to differences in descending control, and instead must be due to changes in intrinsic motor unit excitability within the spinal cord. The authors simply assert/assume that "[derecruitment] results from the relative intrinsic excitability of the motor neurons which override the sole impact of the receive synaptic input". This may well be true, but the authors do not provide any evidence for this in the present paper, and to me it seems equally plausible that the reverse is true - that de-recrutiment might influenced by descending control. This line of argumentation therefore seems somewhat circular.

When subjects were asked to reach TIII, which required the sole activation of a higher threshold MU, subjects almost exclusively chose to activate both MUs first before switching off the lower threshold MU. It may be that the lower de-recruitment threshold of MU2 was determined by descending inputs changing the excitability of either MU1 or MU2 (for example, see J. Nielsen, C. Crone, T. Sinkjær, E. Toft, and H. Hultborn, “Central control of reciprocal inhibition during fictive dorsiflexion in man,” Exp. brain Res., vol. 104, no. 1, pp. 99–106, Apr. 1995 or E. Jankowska, “Interneuronal relay in spinal pathways from proprioceptors,” Prog. Neurobiol., vol. 38, no. 4, pp. 335–378, Apr. 1992). Even if that is the case, it remains unknown why such a command channel that potentially changes the excitability of a single MU was not voluntarily utilized at the initial recruitment to allow for direct movement towards TIII (as direct movement was preferred for TI and TII). We cannot rule out that de-recruitment was affected by selective descending commands. However, our results match observations made in previous studies on intrinsic changes of MU excitability after MU recruitment. Therefore, even if descending pathways were utilized throughout the experiment to change, for example, MU excitability, subjects were not able to explore such pathways to change initial recruitment and achieve general flexible control over MUs. The updated discussion explains this line of reasoning.

Reviewer #4 (Public Review):

[...]

1. Figure 6a nicely demonstrates the strategy used by subjects to hit target TIII. In this example, MU2 was both recruited and de-recruited after MU1 (which is the opposite of what one would expect based on the standard textbook description). The authors state (page 17, line 15-17) that even in the reverse case (when MU2 is de-recruited before MU1) the strategy still leads to successful performance. I am not sure how this would be done. For clarity, the authors could add a panel similar to panel A to this figure but for the case where the MU pairs have the opposite order of de-recruitment.

We have added more examples of successful TIII-instructed trials in Supplement 4. Supplement 4C and D illustrate examples of subjects navigating the cursor inside TIII even when MU2 was de-recruited before MU1. As exemplarily shown, subjects also used the three-stage approach discussed in the manuscript. In contrast to successful trials in which MU2 was de-recruited after MU1 (for example, Supplement 4B), subjects required multiple attempts until finding a precise force level that allowed a continuous firing of MU2 while MU1 remained silent. We have added a possible explanation for such behaviour in the Discussion.

1. The authors discuss a possible type of flexible control which is not evident in the recruitment order of MUs (page 19, line 27-28). This reasoning was not entirely clear to me. Specifically, I was not sure which of the results presented here needs to be explained by such mechanism.

We have shown that subjects can decorrelate the discharge activity of MU1 and MU2 once both MUs are active (e.g. reaching TIII). Thus, flexible control of the MU pair was possible after the initial recruitment. Therefore, this kind of control seems strongly linked to a specific activation state of both MUs. We further elaborated on which potential mechanisms may contribute to this state-dependent control.

1. The authors argue that using a well-controlled task is necessary for understanding the ability to control the descending input to MUs. They thus applied a dorsi-flexion paradigm and MU recordings from TA muscles. However, it is not clear to what extent the results obtained in this study can be extrapolated to the upper limb. Controlling the MUs of the upper limb could be more flexible and more accessible to voluntary control than the control of lower limb muscles. This point is crucial since the authors compare their results to other studies (Formento et al., bioRxiv 2021 and Marshall et al., bioRxiv 2021) which concluded in favor of the flexible control of MU recruitment. Since both studies used the MUs of upper limb muscles, a fair comparison would involve using a constrained task design but for upper limb muscles.

We agree with the reviewer that our work differs from previous approaches, which also studied flexible MU control. We, therefore, added a paragraph to the limitation section of the Discussion.

1. The authors devote a long paragraph in the discussion to account for the variability in the de-recruitment order. They mostly rely on PIC, but there is no clear evidence that this is indeed the case. Is it at all possible that the flexibility in control over MUs was over their recruitment threshold? Was there any change in de-recruitment of the MUs during learning (in a given recording session)?

The de-recruitment threshold did not critically change when compared before and after the experiment on each day (difference in de-recruitment threshold before and after the experiment: -0.16 ± 2.28% MVC, we have now added this result to the Results section). Deviations from the classical recruitment order may be achieved by temporal (short-lived) changes in the intrinsic excitability of single MUs. We, therefore, extended our discussion on potential mechanisms that may explain the observed variability given all MUs receive the same common input.

1. The need for a complicated performance measure (define on page 5, line 3-6) is not entirely clear to me. What is the correlation between this parameter and other, more conventional measures such as total-movement time or maximal deviation from the straight trajectory? In addition, the normalization process is difficult to follow. The best performance was measured across subjects. Does this mean that single subject data could be either down or up-regulated based on the relative performance of the specific subject? Why not normalize the single-subject data and then compare these data across subjects?

We employed this performance metric to overcome shortcomings of traditional measures such as target hit count, time-to-target or deviation from the straight trajectory. Such problems are described in the illustration below for TIII-instructed trials (blue target). A: the duration of the trial is the same in both examples (left and right); however, on the left, the subject manages to keep the cursor close to the target-of-interest while on the right, the cursor is far away from the target centre of TIII. B: In both images the cursor has the same distance d to the target centre of TIII. However, on the left, the subject manages to switch off MU1 while keeping MU2 active, while on the right, both MUs are active. C: On the left, the subject manages to move the cursor inside the TIII before the maximum trial time was reached, while on the right, the subject moved the cursor up and down, not diverging from the ideal trajectory to the target centre but fails to place the cursor inside TIII within the duration of the trial. In all examples, using only one conventional measure fails to account for a higher performance value in the left scenario than in the right. Our performance metric combines several performance metrics such as time-to-target, distance from the target centre, and the discharge rate ratio between MU1 and MU2 via the angle 𝜑 and thus allows a more detailed analysis of the performance than conventional measures. The normalisation of the performance value was done to allow for a comparison across subjects. The best and worst performance was estimated using synthetic data mimicking ideal movement towards each target (i.e. immediate start from the target origin to the centre of the target, while the normalised discharge rate of the corresponding MU is set to 1). Since the target space is normalised for all subjects in the same manner (mean discharge rate of the corresponding MUs at 10 %MVC) this allows us to compare the performance between subjects, conditions and targets.

1. Figure 3C appears to indicate that there was only moderate learning across days for target TI and TII. Even for target TIII there was some improvement but the peak performance in later days was quite poor. The fact that the MUs were different each day may have affected the subjects' ability to learn the task efficiently. It would be interesting to measure the learning obtained on single days.

We have added an analysis that estimated the learning within a session per subject and target (Supplement 3C). In order to evaluate the strength of learning within-session, the Spearman correlation coefficient between target-specific performance and consecutive trials was calculated and averaged across conditions and days. The results suggest that there was little learning within sessions and no significant difference between targets. These results have now been added to the manuscript.

1. On page 16 line 12-13, the authors describe the rare cases where subjects moved directly towards TIII. These cases apparently occurred when the recruitment threshold of MU2 was lower. What is the probable source of this lower recruitment level in these specific trials? Was this incidental (i.e., the trial was only successful when the MU threshold randomly decreased) or was there volitional control over the recruitment threshold? Did the authors test how the MU threshold changed (in percentages) over the course of the training day?

We did not track the recruitment threshold throughout the session but only at the beginning and end. We could not identify any critical changes in the recruitment order (see Results section). However, our analysis indicated that during direct movements towards TIII, MU2 (higher threshold MU) was recruited at a lower force level during the initial ramp and thus had a temporary effective recruitment threshold below MU1. It is important to note that these direct movements towards TIII only occurred for pairs of MUs with a similar recruitment threshold (see Figure 6). One possible explanation for this temporal change in recruitment threshold could be altered excitability due to neuromodulatory effects such as PICs (see Discussion). We have added an analysis that shows that direct movements towards TIII occurred in most cases (>90%) after a preceding TII- or TIIIinstructed trial. Both of these targets-of-interest require activation of MU2. Thus, direct movement towards TIII was likely not the result of specific descending control. Instead, this analysis suggests that the PIC effect triggered at the preceding trial was not entirely extinguished when a trial ending in direct movement towards TIII started. Alternatively, the rare scenarios in which direct movements happened could be entirely random. Similar observations were made in previous biofeedback studies [31]. To clarify these points, we altered the manuscript.

Author Response

Reviewer #2 (Public Review):

Summary: This substantial collaborative effort utilized virus-based retrograde tracing from cervical, thoracic and lumbar spinal cord injection sites, tissue clearing and cutting-edge imaging to develop a supraspinal connectome or map of neurons in the brain that project to the spinal cord. The need for such a connectome-atlas resource is nicely described, and the combination of the actual data with the means to probe that data is truly outstanding.

They then compared the connectome from intact mice to those of mice with mild, moderate and severe spinal cord injuries to reveal the neuronal populations that retain axons and synapses below the level of injury. Finally, they look for correlations between the remaining neuronal populations and functional recovery to reveal which are likely contributing to recovery and its variability after injury. Overall, they successfully achieve their primary goals with the following caveats: The injury model chosen is not the most widely employed in the field, and the anatomical assessment of the injuries is incomplete/not ideal.

Concerns/issues:

1) I would like to see additional discussion/rationale for the chosen injury model and how it compares to other more commonly employed animal models and clinical injuries. Please relate how what is being observed with the supraspinal connectome might be different for these other models and for clinical injuries.

We have added text to the Results and Discussion to explain our rationale for selecting the crush injury model, and to acknowledge differences between this model and more clinically relevant contusion models. (Results: line 360-364, Discussion 608-615). We agree wholeheartedly that a critical future direction will be to deploy brain-wide quantification in contusion models, and we are currently seeking funding to obtain the needed equipment.

2) The assessment of the thoracic injuries employed is not ideal because it provides no anatomical description of spared white matter (or numbers of spared axons) at the injury epicenter.

We address this more fully in the related point below. Briefly, we agree with a need to improve the assessment of the lesion but are hampered by tissue availability. We are unable to assess white matter sparing but can offer quantification of the width of residual astrocyte tissue bridges in four spinal sections from each animal (new Figure 5 – figure supplement 3). As discussed below, however, we recognize the limitations of the lesion assessment and agree with the larger point that the current quantification methods do not position us to make claims about the relative efficacy of spinal injury analyses versus whole-brain sparing analyses to stratify severity or predict outcomes. Our approach should be seen as a complement, not a substitute, for existing lesion-based analyses. We have edited language throughout the manuscript to make this position clearer.

3) Related to this, but an issue that requires separate attention is the highly variable appearance of the injury and tracer/virus injection sites, the variability in the spatial relationship with labeled neurons (lumbar) and how these differences could influence labeling, sprouting of axons of passage and interpretation of the data. In particular this is referring to the data shown in Figure 6 (and related data).

It is true that there is some variability in the relative position of the injury and injection, a surgical reality. The degree of variability was perhaps exaggerated in the original Figure 6 (Now Figure 5), in which one image came from one of two animals in the cohort with a notably larger gap between the injury and injection. Nevertheless, this comment raises the important question of how variability in injection-to-injury distance might affect supraspinal label. First, we would emphasize the data in Figure 1 – Figure Supplement 6, in which we showed that the number of retrogradely labeled supraspinal neurons is relatively stable as injection sites are deliberately varied across the lower thoracic and lumbar cord. Indeed, the question raised here is precisely the reason we performed this early test to determine how sensitive the results might be to shifts in segmental targeting. The results indicate that retrograde labeling is fairly insensitive to L1 versus L4 targeting. As an additional check for this specific experiment we also measured the distance between the rostral spread of viral label and the caudal edge of the lesion and plotted it against the total number of retrogradely labeled neurons in the brain. If a smaller injury/injection gap favored more labeling we might expect negative correlation, but none is apparent. We conclude that although the injury/injection distance did vary in the experiment, it likely did not exert a strong influence on retrograde labeling.

Reviewer #3 (Public Review):

In this manuscript, Wang et al describe a series of experiments aimed at optimizing the experimental and computational approach to the detection of projection-specific neurons across the entire mouse brain. This work builds on a large body of work that has developed nuclear-fused viral labelling, next-generation fluorophores, tissue clearing, image registration, and automated cell segmentation. They apply their techniques to understand projection-specific patterns of supraspinal neurons to the cervical and lumbar spinal cord, and to reveal brain and brainstem connections that are preferentially spared or lost after spinal cord injury.

Strengths:

Although this work does not put forward any fundamentally new methodologies, their careful optimization of the experimental and quantification process will be appreciated by other laboratories attempting to use these types of methods. Moreover, the observations of topological arrangement of various supraspinal centres are important and I believe will be interesting to others in the field.

The web app provided by the authors provides a nice interface for users to explore these data. I think this will be appreciated by people in the field interested in what happens to their brain or brainstem region of interest.

Weaknesses:

Overall the work is well done; however, some of the novelty claims should be better aligned with the experimental findings. Moreover, the statistical approaches put forward to understand the relationship between spinal cord injury severity and cell counts across the mouse brain needs to be more carefully considered.

The authors state that they provide an experimental platform for these types of analysis to be done. My apologies if I missed it but I could not find anywhere the information on viral construct availability or code availability to reproduce the results. Certainly both of these aspects would be required for people to replicate the pipeline. Moreover, the described methodology for imaging and processing is quite sparse. While I appreciate that this information is widely provided in papers that have developed these methods, I do not think it is appropriate to claim to have provided a platform for people to enable these types of analyses without a more in-depth description of the methods. Alternatively, the authors could instead focus on how they optimized current methodologies and avoid the overstatement that this work provides a tool for users. The exception to this is of course the viral constructs, the plasmids of which should be deposited.

We agree that we have not provided a tool per se, more of an example that could be followed. We have revised language in the abstract, introduction, and discussion to make it clear that we optimized existing methods and provide an example of how this can be done, but are not offering a “plug and play” solution to the problem of registration that would, for example, allow upload of external data. For example, in the abstract we replaced “We now provide an experimental platform” with “Here we assemble an experimental workflow.” (Line 28). The term “platform” no longer appears in the manuscript and has been replaced throughout by “example.” We how this matches the intention of the comment and are happy to revise further as needed. Note that the plasmids have been deposited to Addgene.

It was not completely to me clear why or when the authors switch back and forth between different resolutions throughout the manuscript. In the abstract it states that 60 regions were examined, but elsewhere the number is as many as 500. My understanding is that current versions of the Allen Brain Annotation include more than 2000 regions. I think it would make things clear for the readers if a single resolution was used throughout, or at least justified narratively throughout the text to avoid confusion.

Thank you for pointing this out. The Cellfinder application recognizes 645 discrete regions in the brain, and across all experiments we detected supraspinal nuclei in 69 of these. This number, however, includes some very fine distinctions, for example three separate subregions of vestibular nuclei, three subregions of the superior olivary complex, etc. True experts may desire this level of information, but with the goal of accessibility we find it useful to collapse closely related / adjacent regions to an umbrella term. Doing so generates a list of 25 grouped or summary regions. In the revised version we move the 69-region data completely to the supplemental data (there for the experts who wish to parse), and use the consistent 25-region system (plus cervical spinal cord in later sections) to present data in the main figures. We have added text to the Results section (lines 157-162) to clarify this grouping system.

The others provide an interesting analysis of the difference between cervical and lumbar projections. I think this might be one of the more interesting aspects of the paper - yet I found myself a bit confused by the analysis, and whether any of the differences observed were robust. Just prior to this experiment the authors provide a comparison of the mScarlet vs. the mGL, and demonstrate that mGL may label more cells. Yet, in the cervical vs. lumbar analysis it appears they are being treated 1 to 1. Moreover, I could not find any actual statistical analysis of this data? My impression would be that given the potential difference in labelling efficiency between the mScarlet and mGL this should be done using some kind of count analysis that takes into account the overall number of neurons labelled, such as a Chi-sq test or perhaps something more sophisticated. Then, with this kind of statistical analysis in place, do any of the discussed differences hold up? If not, I do not think this would detract from the interesting topological observations - but would call on the authors to be a bit more conservative about their statements and discussion regarding differences in the proportions of neurons projecting to certain supraspinal centers.

This is an important point. In response to this input and related comments from other reviewers we performed new experiments to assess co-localization. The new data address the point above by including quantification of the degree of colocalization that results from titer-matched co-injection of the two fluorophores, providing baseline data. The results of this can be found in Figure 3 – figure supplement 3 and form the basis for statistical comparisons to experimental animals shown in Figure 3.

Finally, I do have some concerns about the author's use of linear regression in their analysis of brain regions after varying severities of SCI. First of all, the BMS score is notoriously non-linear. Despite wide use of linear regressions in the field to attempt to associate various outcomes to these kinds of ordinal measures, this is not appropriate. Some have suggested a rank conversion of the BMS prior to linear analyses, but even this comes with its own problems. Ultimately, the authors have here 2-3 clear cohorts of behavioral scores and drawing a linear regression between these is unlikely to be robustly informative. Moreover, it is unclear whether the authors properly adjusted their p-values from running these regressions on 60 (600?) regions. Finally, the statement in the abstract and discussion that the authors "explain more variability" compared to typical lesion severity analysis is also unsupported. My suggestion would be the following:

Remove the linear regression analyses associated with BMS. I do not think these add value to the paper, and if anything provide a large window of false interpretation due to a violation of the assumptions of this test.

Consider adding a more appropriate statistical analysis of the brain regions, such as a non-parametric group analysis. Knowing which brain regions are severity dependent, and which ones are not, would already be an interesting finding. This finding would not be confounded by any attempt to link it to crude measures of behavior.

We agree that the linear regression approach was flawed and appreciate the opportunity to correct it. After consultation with two groups of statisticians we were forced to conclude that the data are simply underpowered for mixed model and ranking approaches. We therefore adopted a much simpler strategy. As you point out (and as noted by the statisticians), the behavioral data are bimodal; one group of animals regained plantar stepping ability, albeit with varying degrees of coordination (BMS 6-8), while the others showed at most rare plantar steps (BMS 0-3.5). We therefore asked whether the number of spared neurons in each brain region differed between the two groups and also examined the degree of “overlap” in the sparing values between the two groups. The data are now presented in Figure 6.

If the authors would like to state anything about 'explaining more variability' then the proper statistical analysis should be used, which in this case would be to compare the models using a LRT or equivalent. However, as I mentioned it does not seem to be appropriate to be doing this with linear models so the authors should consider a non-linear equivalent if they choose to proceed with this.

We thank the reviewer for the excellent suggestion. However as we explained above after consultation with two groups of statisticians we were forced to conclude that the data are underpowered and could not apply some of the methods suggested. Especially in light of our simplified analysis, we think it is better to remove any claims of the relative success of the sparing in different regions to explain more or less variability. Instead we can simply report that sparing in some regions, but not others, is significantly different between “low-performing” and “high-performing” groups.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors find CpGs within 500Kb of a gene that associate with transcript abundance (cis-eQTMs) in children from the HELIX study. There is much to admire about this work. With two notable exceptions, their work is solid and builds/improves on the work that came before it. Their catalogue of eQTMs could be useful to many other researchers that utilize methylation data from whole blood samples in children. Their annotation of eQTMs is well thought out and exhaustive. As this portion of the work is descriptive, most of their methods are appropriate.

Unfortunately, their use of results from a model that does not account for cell-type proportions across samples diminishes the utility and impact of their findings. I believe that their catalog of eQTMs contains a great deal of spurious results that primarily represent the differences in cell-type proportions across samples.

Lastly, the authors postulate that the eQTM gene associations found uniquely in their unadjusted model (in comparison to results from a model that does account for cell type proportion) represent cell-specific associations that are lost when a fully-adjusted model is assumed. To test this hypothesis, the authors appear to repurpose methods that were not intended for the purposes used in this manuscript. The manuscript lacks adequate statistical validation to support their repurposing of the method, as well as the methodological detail needed to peer review it. This section is a distraction from an otherwise worthy manuscript. But provide evidences that enriched for cell sp CpGs.

Major points

1. Line 414-475: In this section, the authors are suggesting that CpGs that are significant without adjusting for cell type are due to methylation-expression associations that are found only in one cell type, while association found in the fully adjusted model are associations that are shared across the cell types. I do not agree with this hypothesis, as I do not agree that the confounding that occurs when cell-type proportions are not accounted for would behave in this way. Although restricting their search for eQTMs to only those CpGs proximal to a gene will reduce the number of spurious associations, a great deal of the findings in the authors' unadjusted model likely reflect differences in cell-type proportions across samples alone. The Reinius manuscript, cited in this paper, indicates that geneproximal CpGs can have methylation patterns that vary across cell types.

Following reviewers’ recommendations, we have reconsidered our initial hypothesis about the role of cellular composition in the association between methylation and gene expression. Although we still think that some of the eQTMs only found in the model unadjusted for cellular composition could represent cell specific effects, we acknowledge that the majority might be confounded by the extensive gene expression and DNA methylation differences between cell types. Also, we recognize that more sophisticated statistical tests should be applied to prove our hypothesis. Because of this, we have decided to report the eQTMs of the model adjusted for cellular composition in the main manuscript and keep the results of the model unadjusted for cellular composition only in the online catalogue.

1. Line 476-488: Their evidence due to F-statistics is tenuous. The authors do not give enough methodological detail to explain how they're assessing their hypothesis in the results or methods (lines 932-946) sections. The methods they give are difficult to follow. The results in figure S19A are not compelling. The citation in the methods (by Reinius) do not make sense, because Reinius et al did not use F-statistics as a proxy for cell type specificity. The citation that the authors give for this method in the results does not appear to be appropriate for this analysis, either. Jaffe and Irizarry state that a CpG with a high Fstatistic indicates that the methylation at that CpG varies across cell type. They suggest removing these CpGs from significant results, or estimating and correcting for cell type proportions, as their presence would be evidence of statistical confounding. The authors of this manuscript indicate that they find higher F-statistics among the eQTMs uniquely found in the unadjusted model, which seems to only strengthen the idea that the unadjusted model is suffering from statistical confounding.

We recognize the miss-interpretation of the F-statistic in relation to cellular composition. We have deleted all this part from the updated version of the manuscript.

1. The methods used to generate adjusted p-values in this manuscript are not appropriate as they are written. Further, they are nothing like the methods used in the paper cited by the authors. The Bonder paper used permutations to estimate an empirical FDR and cites a publication by Westra et al for their method (below). The Westra paper is a better one to cite, because the methods are more clear. Neither the Bonder nor the Westra paper uses the BH procedure for FDR.

Westra, H.-J. et al. Systematic identification of trans eQTLs as putative drivers of known disease associations. Nat. Genet. 45, 1238-1243 (2013).

We apologize for this misleading citation. Although Bonder et al applied a permutation approach to adjust for multiple testing, our approach was inspired by the method applied in the GTEx project (GTEx consortium, 2020), using CpGs instead of SNPs. The citation has been corrected in the manuscript. Moreover, we have explained in more detail the whole multiple-testing processes in the Material and Methods section (page 14, line 316):

“To ensure that CpGs paired to a higher number of Genes do not have higher chances of being part of an eQTM, multiple-testing was controlled at the CpG level, following a procedure previously applied in the Genotype-Tissue Expression (GTEx) project (Gamazon et al., 2018). Briefly, our statistic used to test the hypothesis that a pair CpGGene is significantly associated is based on considering the lowest p-value observed for a given CpG and all its pairs Gene (e.g. those in the 1 Mb window centered at the TSS). As we do not know the distribution of this statistic under the null, we used a permutation test. We generated 100 permuted gene expression datasets and ran our previous linear regression models obtaining 100 permuted p-values for each CpG-Gene pair. Then, for each CpG, we selected among all CpG-Gene pairs the minimum p-value in each permutation and fitted a beta distribution that is the distribution we obtain when dealing with extreme values (e.g. minimum) (Dudbridge and Gusnanto, 2008). Next, for each CpG, we took the minimum p-value observed in the real data and used the beta distribution to compute the probability of observing a lower p-value. We defined this probability as the empirical p-value of the CpG. Then, we considered as significant those CpGs with empirical p-values to be significant at 5% false discovery rate using BenjaminiHochberg method. Finally, we applied a last step to identify all significant CpG-Gene pairs for all eCpGs. To do so, we defined a genome-wide empirical p-value threshold as the empirical p-value of the eCpG closest to the 5% false discovery rate threshold. We used this empirical p-value to calculate a nominal p-value threshold for each eCpG, based on the beta distribution obtained from the minimum permuted p-values. This nominal p-value threshold was defined as the value for which the inverse cumulative distribution of the beta distribution was equal to the empirical p-value. Then, for each eCpG, we considered as significant all eCpG-Gene variants with a p-value smaller than nominal p-value.”

References:<br /> GTEx consortium, The GTEx Consortium atlas of genetic regulatory effects across human tissues, Science (2020) Sep 11;369(6509):1318-1330. doi: 10.1126/science.aaz1776.

Reviewer #2 (Public Review):

Strength:

Comprehensive analysis Considering genetic factors such as meQTL and comparing results with adult data are interesting.

We thank the reviewer for his/her positive feedback on the manuscript. We agree that the analysis of genetic data and the comparison with eQTMs described in adults are two important points of the study.

Weakness:

• Manuscript is not summarized well. Please send less important findings to supplementary materials. The manuscript is not well written, which includes every little detail in the text, resulting in 86 pages of the manuscript.

Following reviewers’ comments, we have simplified the manuscript. Now only the eQTMs identified in the model adjusted for cellular composition are reported. In addition, functional enrichment analyses have been simplified without reporting all odds ratios (OR) and p-values, which can be seen in the Figures.

• Any possible reason that the eQTM methylation probes are enriched in weak transcription regions? This is surprising.

Bonder et al also found that blood eQTMs were slightly enriched for weak transcription regions (TxWk). Weak transcription regions are highly constitutive and found across many different cell types (Roadmap Epigenetics Consortium, 2015). However, hematopoietic stem cells and immune cells have lower representation of TxWk and other active states, which may be related to their capacity to generate sub-lineages and enter quiescence.

Given that we analyzed whole blood and that ROADMAP chromatin states are only available for blood specific cell types, each CpG in the array was annotated to one or several chromatin states by taking a state as present in that locus if it was described in at least 1 of the 27 bloodrelated cell types. By applying this strategy we may be “over-representing” TxWk chromatin states, in the case TxWk are cell-type specific. As a result, even if each blood cell type might have few TxWk, many positions can be TxWk in at least one cell type, inflating the CpGs considered as TxWk. This might have affected some of the enrichments.

On the other hand, CpG probe reliability depends on methylation levels and variance. TxWk regions show high methylation levels, which tend to be measured with more error. This also might have impacted the results, however the analysis considering only reliable probes (ICC >0.4) showed similar enrichment for TxWk.

Besides these, we do not have a clear answer for the question raised by the reviewer.

References:

Bonder MJ, Luijk R, Zhernakova D V, Moed M, Deelen P, Vermaat M, et al. Disease variants alter transcription factor levels and methylation of their binding sites. Nat Genet [Internet]. 2017 [cited 2017 Nov 2];49:131–8. Available from: http://www.ncbi.nlm.nih.gov/pubmed/27918535

Roadmap Epigenomics Consortium, Kundaje A, Meuleman W, Ernst J, Bilenky M, Yen A, Heravi-Moussavi A, Kheradpour P, Zhang Z, Wang J, Ziller MJ, Amin V, Whitaker JW, Schultz MD, Ward LD, Sarkar A, Quon G, Sandstrom RS, Eaton ML, Wu YC, Pfenning AR, Wang X, Claussnitzer M, Liu Y, Coarfa C, Harris RA, Shoresh N, Epstein CB, Gjoneska E, Leung D, Xie W, Hawkins RD, Lister R, Hong C, Gascard P, Mungall AJ, Moore R, Chuah E, Tam A, Canfield TK, Hansen RS, Kaul R, Sabo PJ, Bansal MS, Carles A, Dixon JR, Farh KH, Feizi S, Karlic R, Kim AR, Kulkarni A, Li D, Lowdon R, Elliott G, Mercer TR, Neph SJ, Onuchic V, Polak P, Rajagopal N, Ray P, Sallari RC, Siebenthall KT, Sinnott-Armstrong NA, Stevens M, Thurman RE, Wu J, Zhang B, Zhou X, Beaudet AE, Boyer LA, De Jager PL, Farnham PJ, Fisher SJ, Haussler D, Jones SJ, Li W, Marra MA, McManus MT, Sunyaev S, Thomson JA, Tlsty TD, Tsai LH, Wang W, Waterland RA, Zhang MQ, Chadwick LH, Bernstein BE, Costello JF, Ecker JR, Hirst M, Meissner A, Milosavljevic A, Ren B, Stamatoyannopoulos JA, Wang T, Kellis M. Integrative analysis of 111 reference human epigenomes. Nature. 2015 Feb 19;518(7539):317-30. doi: 10.1038/nature14248. PMID: 25693563; PMCID: PMC4530010.

• The result that the magnitude of the effect was independent of the distance between the CpG and the TC TSS is surprising. Could you draw a figure where x-axis is the distance between the CpG site and TC TSS and y-axis is p-value?

As suggested by the reviewer, we have taken a more detailed look at the relationship between the effect size and the distance between the CpG and the TC’s TSS. First, we confirmed that the relative orientation (upstream or downstream) did not affect the strength of the association (p-value=0.68). Second, we applied a linear regression between the absolute log2 fold change and the log10 of the distance (in absolute value), finding that they were inversely related. We have updated the manuscript with this information (page 22, line 504):

“We observed an inverse linear association between the eCpG-eGene’s TSS distance and the effect size (p-value = 7.75e-9, Figure 2B); while we did not observe significant differences in effect size due to the relative orientation of the eCpG (upstream or downstream) with respect to the eGene’s TSS (p-value = 0.68).”

Results are shown in Figure 2B. Of note, we winsorized effect size values in order to improve the visualization. The winsorizing process is also explained in Figure 2 legend. Moreover, we have done the plot suggested by the reviewer (see below). It shows that associations with smallest p-values are found close to the TC’s TSS. Nonetheless, as this pattern is also observed for the effect sizes, we have decided to not include it in the manuscript.

• Concerned about too many significant eQTMs. Almost half of genes are associated with methylation. I wonder if false positives are well controlled using the empirical p-values. Using empirical p-value with permutation may mislead since especially you only use 100 permutations. I wonder the result would be similar if they compare their result with the traditional way, either adjusting p-values using p-values from entire TCs or adjusting pvalues using a gene-based method as commonly used in GWAS. Compare your previous result with my suggestion for the first analysis.

Despite the number of genes (TCs) whose expression is associated with DNA methylation is quite high, we do not think this is due to not correctly controlling false positives. Our approach is based on the method used by GTEx (GTEx consortium) and implemented in the FastQTL package (Ongen et al. 2016), to control for positives in the eQTLs discovery. As in GTEx, we run 100 permutations to estimate the parameters of a beta distribution, which we used to model the distribution of p-values for each CpG. Then, to correct for the number of TCs among significant CpGs, we applied False Discovery Rate (FDR) at a threshold < 0.05. Finally, we defined the final set of significant eQTMs using the beta distribution defined in a previous step.

For illustration, we compared the number of eQTMs with our approach to what we would obtain by uniquely applying the FDR method (adjusted p-value <0.05), getting fewer associations with our approach: eQTMs (45,203 with FDR vs 39,749 with our approach), eCpGs (24,611 vs 21,966) and eGenes (9,937 vs 8,886). Among the 8,886 significant eGenes, 6,288 of them are annotated to coding genes, thus representing 27% of the 23,054 eGenes coding for a gene included in the array.

References:

GTEx consortium, The GTEx Consortium atlas of genetic regulatory effects across human tissues, Science (2020) Sep 11;369(6509):1318-1330. doi: 10.1126/science.aaz1776.

Ongen et al. Fast and efficient QTL mapper for thousands of molecular phenotypes, Bioinformatics (2016) May 15;32(10):1479-85. doi: 10.1093/bioinformatics/btv722. Epub 2015 Dec 26.

• I recommend starting with cell type specific results. Without adjusting cell type, the result doesn't make sense.

As suggested by other reviewers, we have withdrawn the model unadjusted for cellular composition.

Reviewer #3 (Public Review):

Although several DNA methylation-gene expression studies have been carried out in adults, this is the first in children. The importance of this is underlined by the finding that surprisingly few associations are observed in both adults and children. This is a timely study and certain to be important for the interpretation of future omic studies in blood samples obtained from children.

We agree with the reviewer that eQTMs in children are important for interpreting EWAS findings conducted in child cohorts such as those of the Pregnancy And Childhood Epigenetics (PACE) consortium.

It is unfortunate that the authors chose to base their reporting on associations unadjusted for cell count heterogeneity. They incorrectly claim that associations linked to cell count variation are likely to be cell-type-specific. While possible, it is probably more likely that the association exists entirely due to cell type differences (which tend to be large) with little or no association within any of the cell types (which tend to be much smaller). In the interests of interpretability, it would be better to report only associations obtained after adjusting for cell count variation.

Following reviewers’ recommendations, we have reconsidered our initial hypothesis about the role of cellular composition in the association between methylation and gene expression. Although we still think that some of the eQTMs only found in the model unadjusted for cellular composition could represent cell specific effects, we acknowledge that the majority might be confounded by the extensive gene expression and DNA methylation differences between cell types. Also, we recognize that more sophisticated statistical tests should be applied to prove our hypothesis. Because of this we have decided to report the eQTMs of the model adjusted for cellular composition in the main manuscript and keep the results of the model unadjusted for cellular composition only in the online catalogue.

Several enrichments could be related to variation in probe quality across the DNA methylation arrays.

For example, enrichment for eQTM CpG sites among those that change with age could simply be due to the fact age and eQTM effects are more likely to be observed for CpG sites with high quality probes than low quality probes. It is more informative to instead ask if eQTM CpG sites are more likely to have increasing rather than decreasing methylation with age. This avoids the probe quality bias since probes with positive associations with age would be expected to have roughly the same quality as those with negative associations with age. There are several other analyses prone to the probe quality bias.

See answer to question 2, below.

Author Response:

Reviewer #1:

This work provides insight into the effects of tetraplegia on the cortical representation of the body in S1. By using fMRI and an attempted finger movement task, the researchers were able to show preserved fine-grained digit maps - even in patients without sensory and motor hand function as well as no spared spinal tissue bridges. The authors also explored whether certain clinical and behavioral determinates may contribute to preserving S1 somatotopy after spinal cord injury.

Overall I found the manuscript to be well-written, the study to be interesting, and the analysis reasonable. I do, however, think the manuscript would benefit by considering and addressing two main suggestions.

1) Provide additional context / rationale for some of the methods. Specific examples below:

a) The rationale behind using the RSA analysis seemed to be predicated on the notion that the signals elicited via a phase-encoded design can only yield information about each voxel's preferred digit and little-to-no information about the degree of digit overlap (see lines 163-166 and 571-575). While this is the case for conventional analyses of these signals, there are more recently developed approaches that are now capable of estimating the degree of somatotopic overlap from phase-encoded data (see: Da Rocha Amaral et al., 2020; Puckett et al., 2020). Although I personally would be interested in seeing one of these types of analyses run on this data, I do not think it is necessary given the RSA data / analysis. Rather, I merely think it is important to add some context so that the reader is not misled into believing that there is no way to estimate this type of information from phase-encoded signals. - Da Rocha Amaral S, Sanchez Panchuelo RM, Francis S (2020) A Data-Driven Multi-scale Technique for fMRI Mapping of the Human Somatosensory Cortex. Brain Topogr 33 (1):22-36. doi:10.1007/s10548-019-00728-6 - Puckett AM, Bollmann S, Junday K, Barth M, Cunnington R (2020) Bayesian population receptive field modeling in human somatosensory cortex. Neuroimage 208:116465. doi:10.1016/j.neuroimage.2019.116465

We did not intend to give the impression that inter-finger overlap can only be estimated using RSA. To clarify this, we included a sentence in our methods section stating that inter-finger overlap cannot be estimated using the traditional travelling wave approach, but new methods have estimated somatotopic overlap from travelling wave data. Since our RSA approach lends itself for estimating inter-finger overlap and is currently the gold standard in characterizing these representational patterns, we opt –in accordance with the reviewer’s comment– not to include this additional analysis.

Revised text Methods:

“While the traditional traveling wave approach is powerful to uncover the somatotopic finger arrangement, a fuller description of hand representation can be obtained by taking into account the entire fine-grained activity pattern of all fingers. RSA-based inter-finger overlap patterns have been shown to depict the invariant representational structure of fingers better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). RSA-based measures are furthermore not prone to some of the problems of measurements of finger selectivity (e.g., dependence on map thresholds). The most common approach for investigating inter-finger overlap is RSA, as used here, though note that somatotopic overlap has recently been estimated from travelling wave data using an iterated Multigrid Priors (iMGP) method and population receptive field modelling (Da Rocha Amaral et al., 2020; Puckett et al., 2020).”

b. The rationale for using minimally thresholded (Z>2) data for the Dice overlap analysis as opposed to the threshold used in data visualization (q<0.05) was unclear. Providing the minimally thresholded maps (in Supplementary) would also aid interpretation of the Dice overlap results.

We followed previously published procedures for calculating the Dice overlap between the two split-halves of the data (Kikkert et al., 2016; J. Kolasinski et al., 2016; Sanders et al., 2019). We used minimally thresholded data to calculate the dice overlap to ensure that our analysis was sensitive to overlaps that would be missed when using high thresholds. We clarified this in the revised manuscript. We thank the reviewer for their suggestion to add a Figure displaying the minimally thresholded split-half hard-edged finger maps - we have added this to the revised manuscript as Figure 2-Figure supplement 1.

To ensure that our thresholding procedure did not change the results of the dice overlap analysis, we repeated this analysis using split-half maps that were thresholded using a q < 0.05 FDR criterion (as was used to create the travelling wave maps in Figures 2A-B). We found the same results as when using the Z >2 thresholding criterion: Overall, split-half consistency was not significantly different between patients and controls, as tested using a robust mixed ANOVA (F(1,17.69) = 0.08, p = 0.79). There was a significant difference in split- half consistency between pairs of same, neighbouring, and non-neighbouring fingers (F(2,14.77) = 38.80, p < 0.001). This neighbourhood relationship was not significantly different between the control and patient groups (i.e., there was no significant interaction; F(2,14.77) = 0.12, p = 0.89). We have included this analysis and the relating figure as Figure 2- Figure supplement 2 in the revised manuscript.

Revised text Methods:

“We followed previously described procedures for calculating the DOC between two halves of the travelling wave data (Kikkert et al., 2016; Kolasinski et al., 2016; Sanders et al., 2019). The averaged finger-specific maps of the first forward and backward runs formed the first data half. The averaged finger-specific maps of the second forward and backward runs formed the second data half. The finger-specific clusters were minimally thresholded (Z>2) on the cortical surface and masked using an S1 ROI, created based on Brodmann area parcellation using Freesurfer (see Figure 2– figure supplement 1 for a visualisation of the minimally thresholded split-half hard-edged finger maps used to calculate the DOC). We used minimally thresholded finger-specific clusters for the DOC analysis to ensure we were sensitive to overlaps that would be missed when using high thresholds. Note that results were unchanged when thresholding the finger-specific clusters using an FDR q < 0.05 criterion (see Figure 2 – figure supplement 2).”

2) Provide a more thorough discussion - particularly with respect to the possible role of top-down processes (e.g., attention).

a) The authors discuss a few potential signal sources that may contribute to the maintenance of (and ability to measure) the somatotopic maps; however, the overall interpretation seems a bit "motor efferent heavy". That is, it seems the authors favor an explanation that the activity patterns measured in S1 were elicited by efference copies from the motor system and that occasional corollary discharges or attempted motor movements play a role in their maintenance over time. The authors consider other explanations, noting - for example - the potential role of attention in preserving the somatotopic representations given that attention has been shown to be able to activate S1 hand representations. The mention of this was, however, rather brief - and I believe the issue deserves a bit more of a balanced consideration.

When the authors consider the possible role of attention in maintaining the somatotopic representations (lines 329-333), they mention that observing others' fingers being touched or attending to others' finger movements may contribute. But there is no mention of attending to one's own fingers (which has been shown to elicit activity as cited). I realize that the patients lack sensorimotor function (and hence may find it difficult to "attend" to their fingers); however, they have all had prior experience with their fingers and therefore might still be able to attend to them (or at least the idea of their digits) such that activity is elicited. For example, it is not clear to me that it would be any more difficult for the patients to be asked to attend to their digits compared to being asked to attempt to move their digits. I would even suggest that attempting to move a digit (regardless of whether you can or not) requires that one attends to the digit before attempting to initiate the movement as well as throughout the attempted motor movement. Because of this, it seems possible that attention-related processes could be playing a role in or even driving the signals measured during the attempted movement task - as well as those involved in the ongoing maintenance of the maps after injury. I don't think this possibility can be dismissed given the data in hand, but perhaps the issue could be addressed by a bit more thorough of a discussion on the process of "attempting to move" a digit (even one that does not move) - and the various top-down processes that might be involved.

We thank the reviewer for their consideration and insights into the potential mechanisms underlying our results. We have now elaborated further on the possibility that attention- related processes might have contributed to the reported effects, also in consideration of comment 3.4.

Revised text Discussion:

“Spared spinal cord tissue bridges can be found in most patients with a clinically incomplete injury, their width being predictive of electrophysiological information flow, recovery of sensorimotor function, and neuropathic pain (Huber et al., 2017; Pfyffer et al., 2021, 2019; Vallotton et al., 2019). However, in this study, spared midsagittal spinal tissue bridges at the lesion level, motor function, and sensory function did not seem necessary to maintain and activate a somatotopic hand representation in S1. We found a highly typical hand representation in two patients (S01 and S03) who did not have any spared spinal tissue bridges at the lesion level, a complete (S01) or near complete (S03) hand paralysis, and a complete (S01) or near complete loss (S03) of hand sensory function. Our predictive modelling results were in line with this notion and showed that these behavioural and structural spinal cord determinants were not predictive of hand representation typicality. Note however that our sample size was limited, and it is challenging to draw definite conclusions from non-significant predictive modelling results.”

“How may these representations be preserved over time and activated through attempted movements in the absence of peripheral information? S1 is reciprocally connected with various brain areas, e.g., M1, lateral parietal cortex, poster parietal area 5, secondary somatosensory cortex, and supplementary motor cortex (Delhaye et al., 2019). After loss of sensory inputs and paralysis through SCI, S1 representations may be activated and preserved through its interconnections with these areas. Firstly, it is possible that cortico-cortical efference copies may keep a representation ‘alive’ through occasional corollary discharge (London and Miller, 2013). While motor and sensory signals no longer pass through the spinal cord in the absence of spinal tissue bridges, S1 and M1 remain intact. When a motor command is initiated (e.g., in the form of an attempted hand movement) an efference copy is thought to be sent to S1 in the form of corollary discharge. This corollary discharge resembles the expected somatosensory feedback activity pattern and may drive somatotopic S1 activity even in the absence of ascending afferent signals from the hand (Adams et al., 2013; London and Miller, 2013). It is possible that our patients occasionally performed attempted movements which would result in corollary discharge in S1. Second, it is likely that attempting individual finger movements poses high attentional demands on tetraplegic patients. Accordingly, attentional processes might have contributed to eliciting somatotopic S1 activity. Evidence for this account comes from studies showing that it is possible to activate somatotopic S1 hand representations through attending to individual fingers (Puckett et al., 2017) or through touch observation (Kuehn et al., 2018). Attending to fingers during our attempted finger movement task may have been sufficient to elicit somatotopic S1 activity through top-down processes in the tetraplegic patients who lacked hand motor and sensory function. Furthermore, one might speculate that observing others’ or one’s own fingers being touched or directing attention to others’ hand movements or one’s own fingers may help preserve somatotopic representations. Third, it is possible that these somatotopic maps are relatively hardwired and while they deteriorate over time, they never fully disappear. Indeed, somatotopic mapping of a sensory deprived body part has been shown to be resilient after dystonia (Ejaz et al., 2016; though see Burman et al., (2009) and Taub et al., (1998)) and arm amputation (Bruurmijn et al., 2017; Kikkert et al., 2016; Wesselink et al., 2019). Fourth, it is possible that even though a patient is clinically assessed to be complete and is unable to perceive sensory stimuli on the deprived body part, there is still some ascending information flow that contributes to preserving somatotopy (Wrigley et al., 2018). A recent study found that although complete paraplegic SCI patients were unable to perceive a brushing stimulus on their toe, 48% of patients activated the location appropriate S1 area (Wrigley et al., 2018). However, the authors of this study defined the completeness of patients’ injuries via behavioural testing, while we additionally assessed the retained connections passing through the SCI directly via quantification of spared spinal tissue bridges through structural MRI. It is unlikely that spinal tissue carrying somatotopically organised information would be missed by our assessment (Huber et al., 2017; Pfyffer et al., 2019). Our experiment did not allow us to tease apart these potential processes and it is likely that various processes simultaneously influence the preservation of S1 somatotopy and elicited the observed somatotopic S1 activity.”

Reviewer #2:

The authors investigate SCI patients and characterize the topographic representation of the hand in sensorimotor cortex when asked to move their hand (which controls could do but patients could not). The authors compare some parameters of topographic map organization and conclude that they do not differ between patients and controls, whereas they find changes in the typicality of the maps that decrease with years since disease onset in patients. Whereas these initial analyses are interesting, they are not clearly related to a mechanistic model of the disorder and the underlying pathophysiology that is expected in the patients. Furthermore, additional analyses on more fine-grained map changes are needed to support the authors' claims. Finally, the major result of changed typicality in the patients is in my view not valid.

• Concept 1. At present, there is no clear hypotheses about the (expected or hypothesized) mechanistic changes of the sensorimotor maps in the patients. The authors refer to "altered" maps and repeatedly say that "results are mixed" (3 times in the introduction).

We thank the reviewer for highlighting to us that our introduction and hypotheses were unclear and/or incomplete to them. We have restructured our Introduction to better highlight competing hypotheses on how SCI may change S1 hand representations, the reasons for our analytical approach, and elaborate on our hypotheses.

Revised text Introduction:

“Research in non-human primate models of chronic and complete cervical SCI has shown that the S1 hand area becomes largely unresponsive to tactile hand stimulation after the injury (Jain et al., 2008; Kambi et al., 2014; Liao et al., 2021). The surviving finger-related activity became disorganised such that a few somatotopically appropriate sites but also other somatotopically nonmatched sites were activated (Liao et al., 2021). Seminal nonhuman primate research has further demonstrated that SCI leads to extensive cortical reorganisation in S1, such that tactile stimulation of cortically adjacent body parts (e.g., of the face) activated the deprived brain territory (e.g., of the hand; Halder et al., 2018; Jain et al., 2008; Kambi et al., 2014). Although the physiological hand representation appears to largely be altered following a chronic cervical SCI in non-human primates, the anatomical isomorphs of individual fingers are unchanged (Jain et al., 1998). This suggests that while a hand representation can no longer be activated through tactile stimulation after the loss of afferent spinal pathways, a latent and somatotopic hand representation could be preserved regardless of large-scale physiological reorganisation.

A similar pattern of results has been reported for human SCI patients. Transcranial magnetic stimulation (TMS) studies induced current in localised areas of SCI patient’s M1 to induce a peripheral muscle response. They found that representations of more impaired muscles retract or are absent while representations of less impaired muscles shift and expand (Fassett et al., 2018; Freund et al., 2011a; Levy et al., 1990; Streletz et al., 1995; Topka et al., 1991; Urbin et al., 2019). Similarly, human fMRI studies have shown that cortically neighbouring body part representations can shift towards, though do not invade, the deprived M1 and S1 cortex (Freund et al., 2011b; Henderson et al., 2011; Jutzeler et al., 2015; Wrigley et al., 2018, 2009). Other human fMRI studies hint at the possibility of latent somatotopic hand representations following SCI by showing that attempted movements with the paralysed and sensory deprived body part can still evoke signals in the sensorimotor system (Cramer et al., 2005; Freund et al., 2011b; Kokotilo et al., 2009; Solstrand Dahlberg et al., 2018). This attempted ‘net’ movement activity was, however, shown to substantially differ from healthy controls: Activity levels have been shown to be increased (Freund et al., 2011b; Kokotilo et al., 2009; Solstrand Dahlberg et al., 2018) or decreased (Hotz- Boendermaker et al., 2008), volumes of activation have been shown to be reduced (Cramer et al., 2005; Hotz-Boendermaker et al., 2008), activation was found in somatotopically nonmatched cortical sites (Freund et al., 2011b), and activation was poorly modulated when patients switched from attempted to imagined movements (Cramer et al., 2005). These observations have therefore mostly been attributed to abnormal and/or disorganised processing induced by the SCI. It remains possible though that, despite certain aspects of sensorimotor activity being altered after SCI, somatotopically typical representations of the paralysed and sensory deprived body parts can be preserved (e.g., finger somatotopy of affected hand). Such preserved representations have the potential to be exploited in a functionally meaningful manner (e.g., via neuroprosthetics).

Case studies using intracortical stimulation in the S1 hand area to elicit finger sensations in SCI patients hint at such preserved somatotopic representations (Fifer et al., 2020; Flesher et al., 2016), with one exception (Armenta Salas et al., 2018). Negative results were suggested to be due to a loss of hand somatotopy and/or reorganisation in S1 of the implanted SCI patient or due to potential misplacement of the implant (Armenta Salas et al., 2018). Whether fine-grained somatotopy is generally preserved in the tetraplegic patient population remains unknown. It is also unclear what clinical, behavioural, and structural spinal cord determinants may influence such representations to be maintained. Here we used functional MRI (fMRI) and a visually cued (attempted) finger movement task in tetraplegic patients to examine whether hand somatotopy is preserved following a disconnection between the brain and the periphery. We instructed patients to perform the fMRI tasks with their most impaired upper limb and matched controls’ tested hands to patients’ tested hands. If a patient was unable to make overt finger movements due to their injury, then we carefully instructed them to make attempted (i.e., not imagined) finger movements. To see whether patient’s maps exhibited characteristics of somatotopy, we visualised finger selectivity in S1 using a travelling wave approach. To investigate whether fine-grained hand somatotopy was preserved and could be activated in S1 following SCI, we assessed inter-finger representational distance patterns using representational similarity analysis (RSA). These inter-finger distance patterns are thought to be shaped by daily life experience such that fingers used more frequently together in daily life have lower representational distances (Ejaz et al., 2015). RSA-based inter-finger distance patterns have been shown to depict the invariant representational structure of fingers in S1 and M1 better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). Over the past years RSA has therefore regularly been used to investigate somatotopy of finger representations both in healthy (e.g., Akselrod et al., 2017; Ariani et al., 2020; Ejaz et al., 2015; Gooijers et al., 2021; Kieliba et al., 2021; Kolasinski et al., 2016; Liu et al., 2021; Sanders et al., 2019) and patient populations (e.g., Dempsey-Jones et al., 2019; Ejaz et al., 2016; Kikkert et al., 2016; Wesselink et al., 2019). We closely followed procedures that have previously been used to map preserved and typical somatotopic finger selectivity and inter-finger representational distance patterns of amputees’ missing hands in S1 using volitional phantom finger movements (Kikkert et al., 2016; Wesselink et al., 2019). However, in amputees, these movements generally recruit the residual arm muscles that used to control the missing limb via intact connections between the brain and spinal cord. Whether similar preserved somatotopic mapping can be observed in SCI patients with diminished or no connections between the brain and the periphery is unclear. If finger somatotopy is preserved in tetraplegic patients, then we should find typical inter-finger representational distance patterns in the S1 hand area of these patients. By measuring a group of fourteen chronic tetraplegic patients with varying amounts of spared spinal cord tissue at the lesion level (quantified by means of midsagittal tissue bridges based on sagittal T2w scans), we uniquely assessed whether preserved connections between the brain and periphery are necessary to preserve fine somatotopic mapping in S1 (Huber et al., 2017; Pfyffer et al., 2019). If spared connections between the periphery and the brain are not necessary for preserving hand somatotopy, then we would find typical inter-finger representational distance patterns even in patients without spared spinal tissue bridges. We also investigated what clinical and behavioural determinants may contribute to preserving S1 hand somatotopy after chronic SCI. If spared sensorimotor hand function is not necessary for preserving hand somatotopy, then we would find typical inter-finger representational distance patterns even in patients who suffer from full sensory loss and paralysis of the hand(s).”

They do not in detail report which results actually have been reported before, which is a major problem, because those prior results should have motivated the analyses the authors conducted. For instance, two of the cited studies found that in SCI patients, only ONE FINGER shifted towards the malfunctioning area (i.e., the small finger) whereas all other fingers were the same. However, the authors do NOT perform single finger analyses but always average their results ACROSS fingers. This is even true in spite of some patients indeed showing MISSING FINGERS as is clearly evident in the figure, and in spite of the clearly reduced distance of the thumb in the patients as is also visible in another figure. Nothing of this is seen in the results, because the ANOVA and analyses never have the factor of "finger". Instead, the authors always average the analyses across finger. The conclusion that the maps do not differ is therefore not justified at present. This severely reduces any conclusions that an be drawn from the data at present.

We apologise for the lack of clarity. We now added additional detail regarding studies showing altered sensorimotor processing following SCI. We also clarified that we based our analysis steps on previous studies investigating hand somatotopy following deafferentation (i.e., following arm amputation; Kikkert et al., 2016; Wesselink et al., 2019) and somatotopic reorganisation RSA- based inter-finger distance patterns have been shown to depict the invariant representational structure of fingers in S1 and M1 better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). Over the past years RSA has therefore regularly been used to investigate somatotopy of finger representations both in healthy (e.g., Akselrod et al., 2017; Ariani et al., 2020; Ejaz et al., 2015; Gooijers et al., 2021; Kieliba et al., 2021; Kolasinski et al., 2016; Liu et al., 2021; Sanders et al., 2019) and patient populations (e.g. Dempsey-Jones et al., 2019; Ejaz et al., 2016; Kikkert et al., 2016; Wesselink et al., 2019). It is believed to be the most appropriate measure to reliably detect subtle changes in somatotopy. We adjusted the text in our revised Introduction section to better highlight this.

Please note that we do not average across fingers in our RSA typicality procedure. Instead, RSA considers how the (attempted) movement with one finger changes the activity pattern across the whole hand representation. Note that somatotopic reorganisation will change the inter-finger distance measured with this method as previously shown (Kieliba et al., 2021; Kolasinski et al., 2016; Wesselink et al., 2019).

Still, as per the reviewer’s suggestion, we conducted a robust mixed ANOVA on the RSA distance measures with a within-subjects factor for finger pair (10 levels) and a between- subjects factor for group (2 levels: controls and SCI patients). We did not find a significant group effect (F(1,21.66) = 1.50, p = 0.23). There was a significant difference in distance between finger pairs (F(9,15.38) = 27.22, p < 0.001), but this was not significantly different between groups (i.e., no significant finger pair by group interaction; F(9,15.38) = 1.05, p = 0.45). When testing for group differences per finger pair, the BF only revealed inconclusive evidence (BF > 0.37 and < 1.11; note that we could not run a Bayesian ANOVA due to normality violations). We have added this analysis to the revised manuscript.

Lastly, we would like to highlight that our argument is that the finger maps can be preserved in the absence of sensory and motor function, but over time they deteriorate and become less somatotopic. As such, we do not aim to state that they are unchanged overall – but rather that they can be unchanged even despite loss of sensory and motor function. We have clarified this in our abstract and manuscript to avoid confusion.

Revised abstract:

“Previous studies showed reorganised and/or altered activity in the primary sensorimotor cortex after a spinal cord injury (SCI), suggested to reflect abnormal processing. However,little is knownaboutwhether somatotopically-specific representations can be preserved despite alterations in net activity. In this observational study we used functional MRI and an (attempted) finger movement task in tetraplegic patients to characterise the somatotopic hand layout in primary somatosensory cortex. We further used structural MRI to assess spared spinal tissue bridges. We found that somatotopic hand representations can be preserved in absence of sensory and motor hand functioning, and no spared spinal tissue bridges. Such preserved hand somatotopy could be exploited by rehabilitation approaches that aim to establish new hand-brain functional connections after SCI (e.g., neuroprosthetics). However, over years since SCI the hand representation somatotopy deteriorated, suggesting that somatotopic hand representations are more easily targeted within the first years after SCI.”

Revised text Methods:

“Second, we tested whether the inter-finger distances were different between controls and patients using a robust mixed ANOVA with a within-participants factor for finger pair (10 levels) and a between-participants factor for group (2 levels: controls and patients).”

Revised text Results:

“We then tested whether the inter-finger distances were different across finger pairs between controls and SCI patients using a robust mixed ANOVA with a within-participants factor for finger pair (10 levels) and a between-participants factor for group (2 levels: controls and patients). We did not find a significant difference in inter-finger distances between patients and controls (F(1,21.66) = 1.50, p = 0.23). The inter-finger distances were significantly different across finger pairs, as would be expected based on somatotopic mapping (F(9,15.38) = 27.22, p < 0.001). This pattern of inter-finger distances was not significantly different between groups (i.e., no significant finger pair by group interaction; F(9,15.38) = 1.05, p = 0.45). When testing for group differences per finger pair, the BF only revealed inconclusive evidence (BF > 0.37 and < 1.11; note that we could not run a Bayesian ANOVA due to normality violations).”

Revised text Discussion:

“In this study we investigated whether hand somatotopy is preserved and can be activated through attempted movements following tetraplegia. We tested a heterogenous group of SCI patients to examine what clinical, behavioural, and structural spinal cord determinants contribute to preserving S1 somatotopy. Our results revealed that detailed hand somatotopy can be preserved following tetraplegia, even in the absence of sensory and motor function and a lack of spared spinal tissue bridges. However, over time since SCI these finger maps deteriorated such that the hand somatotopy became less typical.”

• Concept 2: This also relates to the fact that the most prominent and consistent finding of prior studies was to show changes in map AMPLITUDE in the maps of patients. It is not clear to me how amplitude was measured here, because the text says "average BOLD activity". What should be reported are standard measures of signal amplitude both across the map area and for individual fingers.

We apologise for the lack of clarity, “average BOLD activity” represented the average z- standardised activity within the S1 hand ROI. To comply with the reviewer’s comment, we adjusted this to the percent signal change underneath the S1 hand ROI and report this instead in our revised manuscript and in revised Figure 3A and revised Figure 3- Figure supplement 1. Note that results were unchanged.

As per the reviewer’s suggestion, we further extracted the activity levels for individual fingers under finger-specific ROIs. To create finger-specific ROIs, probability finger maps were created based on the travelling wave data of the control group, thresholded at 25% (i.e., meaning that at least 5 out of 18 control participants needed to significantly activate a vertex for this vertex to be included in the ROI), and binarised. We then used the separately acquired blocked design data to extract the corresponding finger movement activity levels underlying these finger-specific ROIs per participant. Per ROI, we then compared the activity level between groups. After correction for multiple comparisons, there was no significant difference between groups for the thumb (U = 93, p = 0.37), index (t(30) = -0.003, p = 0.99), middle (t(30) = 1.11, p = 0.35), ring (t(30) = 2.02, p = 0.13), or little finger (t(30) = 2.14, p = 0.20). We have added this analysis to Appendix 1.

Note that lower or higher BOLD amplitude levels do not influence our typicality scores per se. Indeed, typical inter-finger representational patterns have been shown to persist even in ipsilateral M1 that exhibited a negative BOLD response during finger movements (Berlot et al., 2019). As long as the typical inter-finger relationships are preserved, brain areas that have low amplitudes of activity can have a typical somatotopic representation.

Revised text in Methods:

"The percent signal change for overall task-related activity was then extracted for voxels underlying this S1 hand ROI per participant. A similar analysis was used to investigate overall task-related activity in an M1 hand ROI (see Figure 3- Figure supplement 1). We further compared activity levels in finger-specific ROIs in S1 between groups and conducted a geodesic distance analysis to assess whether the finger representations of the SCI patients were aligned differently and/or shifted compared to the control participants (see Appendix 1)."

Revised text in Results:

“Task-related activity was quantified by extracting the percent signal change for finger movement (across all fingers) versus baseline across within the contralateral S1 hand ROI (see Figure 3A). Overall, all patients were able to engage their S1 hand area by moving individual fingers (t(13)=7.46, p < 0.001; BF10=4.28e +3), as did controls (t(17)=9.92, p < 0.001; BF10=7.40e +5). Furthermore, patients’ task-related activity was not significantly different from controls (t(30)=-0.82, p=0.42; BF10=0.44), with the BF showing anecdotal evidence in favour of the null hypothesis.”

Revised Appendix 1:

“Percent signal change in finger-specific clusters To assess whether finger movement activity levels were different between patients and controls, we created finger-specific ROIs and extracted the activity level of the corresponding finger movement for each participant. To create the finger-specific ROIs, the probability finger surface maps that were created from the travelling wave data of the control group (see main manuscript) were thresholded at 25% (i.e., meaning that at least 5 out of 18 control participants needed to significantly activate a vertex for this vertex to be included in the ROI), and binarised. We then used the separately acquired blocked design data to extract the finger movement activity levels underlying these finger-specific ROIs. We first flipped the contrast images resulting from each participant’s fixed effects analysis (i.e., that was ran to average across the 4 blocked design runs) along the x-axis for the left-hand tested participants. Each participant’s contrast maps were then resampled to the Freesurfer 2D average atlas and the averaged z-standardised activity level was extracted for each finger movement vs rest contrast underlying the finger-specific ROIs. We compared the activity levels for each finger movement in the corresponding finger ROI (i.e., thumb movement activity in the thumb ROI, index finger movement activity in the index finger ROI, etc.) between groups. After correction for multiple comparisons, there was no significant difference between groups for the thumb (U = 93, p = 0.37), index (t(30) = -0.003, p = 0.99), middle (t(30) = 1.11, p = 0.35), ring (t(30) = 2.02, p = 0.13), or little finger (t(30) = 2.14, p = 0.20).”

Appendix 1- Figure 1: Finger-specific activity levels in finger-specific regions of interest. A) Finger- specific ROIs were based on the control group’s binarised 25% probability travelling wave finger selectivity maps. B) Finger movement activity levels in the corresponding finger-specific ROIs. There were no significant differences in activity levels between the SCI patient and control groups. Controls are projected in grey; SCI patients are projected in orange. Error bars show the standard error of the mean. White arrows indicate the central sulcus. A = anterior; P = posterior.

• Concept 3: The authors present a hypothesis on the underlying mechanisms of SCI that does not seem to reflect prior data. The argument is that changes in map alignment relate to maladaptive changes and pain. However, the literature that the authors cite does not support this claim. In fact, Freund 2011 promotes the importance of map amplitude but not alignment, whereas other studies either show no relation of activation to pain, or they even show that map shift relates to LESS pain, i.e., the reverse argument than what the authors say. My impression is that the model that the authors present is mainly a model that is used for phantom pain but not for SCI. Taking this into consideration, the findings the authors present are not surprising anymore, because in fact none of these studies claimed that the affected area should be absent in SCI patients; these papers only say that the other body parts change in location or amplitude, which is something the authors did not measure. It is important to make this clear in the text.

As the reviewer states, the literature is debated regarding the relationship between reorganisation and pain in SCI patients. We did not highlight this clearly enough. To improve clarity and focus our message we have therefore removed the sentence regarding reorganisation and pain from the Introduction of our revised manuscript. Also taking comment 2.1 and 2.2 into consideration, we have restructured our Introduction.

We respectfully disagree with the reviewer that our results are not novel or surprising. Whether the full fine-grained hand somatotopy is preserved following a complete motor and sensory loss through tetraplegia has not been considered before. Furthermore, to our knowledge, there is no paper that has inspected the full somatotopic layout in a heterogenous sample of SCI patients and shown that over time since injury, hand somatotopy deteriorates. We indeed cannot make claims regarding the reorganization in S1 with regards to neighbouring cortical areas activating the hand area, as we have now clarified further in the revised Discussion. We now also clarify in our discussion that our result does not exclude the possibility of reorganisation occurring simultaneously and that this is topic for further investigation. As described in the Discussion, it is very possible that reorganisation and preserved somatotopy could co-occur.

Revised text Discussion:

“We did not probe body parts other than the hand and could therefore not investigate whether any remapping of other (neighbouring and/or intact) body part representations towards or into the deprived S1 hand cortex may have taken place. Whether reorganisation and preservation of the original function can simultaneously take place within the same cortical area therefore remains a topic for further investigation. It is possible that reorganisation and preservation of the original function could co-occur within cortical areas. Indeed, non-human primate studies demonstrated that remapping observed in S1 actually reflects reorganisation in subcortical areas of the somatosensory pathway, principally the brainstem (Chand and Jain, 2015; Kambi et al., 2014). As such, the deprived S1 area receives reorganised somatosensory inputs upon tactile stimulation of neighbouring intact body parts. This would simultaneously allow the original S1 representation of the deprived body part to be preserved, as observed in our results when we directly probed the deprived S1 hand area through attempted finger movements.”

• Concept 4: There is yet another more general point on the concept and related hypotheses: Why do the authors assume that immediately after SCI the finger map should disappear? This seems to me the more unlikely hypotheses compared to what the data seem to suggest: preservation and detoriation over time. In my view, there is no biological model that would suggest that a finger map suddenly disappears after input loss. How should this deterioration be mediated? By cellular loss? As already stated above, the finding is therefore much less surprising as the authors argue.

We did not expect that finger maps would disappear, especially given the case studies using S1 intracortical stimulation studies in SCI patients and the result of preserved somatotopy of the missing hand in amputees. We are not sure which part of the manuscript might have caused this misunderstanding.

With regards to the reviewer’s comment that there are no models to suggest that fingers maps would disappear: there is competing research on this as we now explain in our revised Introduction. Non-human primate research has shown that the S1 hand area becomes largely unresponsive to tactile hand stimulation after an SCI (Jain et al., 2008; Kambi et al., 2014; Liao et al., 2021). The surviving finger-related activity was shown to be disorganised such that a few somatotopically appropriate sites but also other somatotopically nonmatched sites were activated (Liao et al., 2021). These fingers areas in S1 became responsive to touch on the face. Furthermore, TMS studies that induce current in localised areas of M1 to induce a peripheral muscle response in SCI patients have shown that representations of more impaired muscles retract or are absent (Fassett et al., 2018; Freund et al., 2011a; Levy et al., 1990; Streletz et al., 1995; Topka et al., 1991; Urbin et al., 2019). We do not believe that this indicates that the S1 hand somatotopy is lost, but rather that tactile inputs and motor outputs no longer pass the level of injury. Indeed, non-human primate work showing immutable myelin borders between finger representations in S1 post SCI suggests that a latent hand representation may be preserved. Further hints for such preserved somatotopy comes from fMRI studies showing net sensorimotor activity during attempted movements with the paralysed body part, intracortical stimulation studies in SCI patients, and preserved somatotopic maps of the missing hand in amputees. We have restructured our Introduction accordingly, also taking into consideration comments 2.1, 2.2, and 2.4.

• Methods & Results. The authors refer to an analyses that they call "typicality" where they say that they assess how "typical" a finger map is. Given this is not a standard measure, I was wondering how the authors decided what a "typical" finger map is. In fact, there are a few papers published on this issue where the average location of each finger in a large number of subjects is detailed. Rather than referring to this literature, the authors use another dataset from another study of themselves that was conduced on n=8 individuals and using 7T MRI (note that in the present study, 3T MRI was used) to define what "typical" is. This approach is not valid. First, this "typical" dataset is not validated for being typical (i.e., it is not compared with standard atlases on hand and finger location), second, it was assessed using a different MRI field strength, third, it was too little subjects to say that this should be a typical dataset, forth, the group differed from the patients in terms of age and gender (i.e., non-matched group), and fifth, the authors even say that the design was different ("was defined similarly", i.e., not the same). This approach is therefore in my view not valid, particularly given the authors measured age- and gender-matched controls that should be used to compare the maps with the patients. This is a critical point because changes in typicality is the main result of the paper.

We respectfully disagree with the reviewer that the typicality measure is not standard, invalid, and inaccurate. RSA-based inter-finger overlap patterns have been shown to depict the invariant representational structure of fingers better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). RSA-based inter- finger representation measures have been shown to have more within-subject stability (both within the same session and between sessions that were 6 months apart) and less inter-subject variability (Ejaz et al., 2015) than these other measures of somatotopy. RSA-based measures are furthermore not prone to some of the problems of measurements of finger selectivity (e.g., dependence on map thresholds). Indeed, over the past years RSA has become the golden standard to investigate somatotopy of finger representations both in healthy (e.g., Akselrod et al., 2017; Ariani et al., 2020; Ejaz et al., 2015; Gooijers et al., 2021; Kieliba et al., 2021; Kolasinski et al., 2016; Liu et al., 2021; Sanders et al., 2019) and patient populations (e.g. Dempsey-Jones et al., 2019; Ejaz et al., 2016; Kikkert et al., 2016; Wesselink et al., 2019). Moreover, various papers have been published in eLife and elsewhere that used the same RSA-based typicality criteria to assess plasticity in finger representations (Dempsey-Jones et al., 2019; Ejaz et al., 2015; Kieliba et al., 2021; Wesselink et al., 2019). We now highlight this in the revised Introduction.

The canonical RDM used in our study has previously been used as a canonical RDM in a 3T study exploring finger somatotopy in amputees (Wesselink et al., 2019) and was made available to us (note that we did not collect this data ourselves). We aimed to use similar measures as in Wesselink et al (2019) and therefore felt it was most appropriate to use the same canonical RDM. One of the strengths of RSA is it can be used to quantitatively relate brain activity measures obtained using different modalities, across different species, brain areas, brain and behavioural measures etc. (Kriegeskorte et al., 2008). As such, the fact that this canonical RDM was constructed based on data collected using 7T fMRI using a digit tapping task should not influence our results. We however agree with the reviewer it is good to demonstrate that our results would not change when using a canonical RDM based on the average RDM of our age-, sex- and handedness matched control group. We therefore recalculated the typicality of all participants using the controls’ average RDM as the canonical RDM. We found a strong and highly significant correlation in typicality scores calculated using the canonical RDM from the independent dataset and the controls’ average RDM (see figure below). This was true for both the patient (rs = 0.92, p < 0.001; red dots) and control groups (rs = 0.78, p < 0.001; grey dots).

We then repeated all analysis using these newly calculated typicality scores. As expected, we found the same results as when using a canonical RDM based on the independent dataset (see below for details). This analysis has been added to the revised Appendix 1 and is referred to in the main manuscript.

Revised text Introduction:

“To investigate whether fine-grained hand somatotopy was preserved and could be activated in S1 following SCI, we assessed inter-finger representational distance patterns using representational similarity analysis (RSA). These inter-finger distance patterns are thought to be shaped by daily life experience such that fingers used more frequently together in daily life have lower representational distances (Ejaz et al., 2015). RSA-based inter-finger distance patterns have been shown to depict the invariant representational structure of fingers in S1 and M1 better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). Over the past years RSA has therefore regularly been used to investigate somatotopy of finger representations both in healthy (e.g., Akselrod et al., 2017; Ariani et al., 2020; Ejaz et al., 2015; Gooijers et al., 2021; Kieliba et al., 2021; Kolasinski et al., 2016; Liu et al., 2021; Sanders et al., 2019) and patient populations (e.g., Dempsey- Jones et al., 2019; Ejaz et al., 2016; Kikkert et al., 2016; Wesselink et al., 2019). We closely followed procedures that have previously been used to map preserved and typical somatotopic finger selectivity and inter-finger representational distance patterns of amputees’ missing hands in S1 using volitional phantom finger movements (Kikkert et al., 2016; Wesselink et al., 2019).”

Revised text Results:

“This canonical RDM was based on 7T finger movement fMRI data in an independently acquired cohort of healthy controls (n = 8). The S1 hand ROI used to calculated this canonical RDM was defined similarly as in the current study (see Wesselink and Maimon- Mor, (2017b) for details). Note that results were unchanged when calculating typicality scores using a canonical RDM based on the averaged RDM of the age-, sex-, and handedness-matched control group tested in this study (see Appendix 1).”

Revised text Methods:

“While the traditional traveling wave approach is powerful to uncover the somatotopic finger arrangement, a fuller description of hand representation can be obtained by taking into account the entire fine-grained activity pattern of all fingers. RSA-based inter-finger overlap patterns have been shown to depict the invariant representational structure of fingers better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). RSA-based measures are furthermore not prone to some of the problems of measurements of finger selectivity (e.g., dependence on map thresholds).”

“Third, we estimated the somatotopic typicality (or normality) of each participant’s RDM by calculating a Spearman correlation with a canonical RDM. We followed previously described procedures for calculating the typicality score (Dempsey-Jones et al., 2019; Ejaz et al., 2015; Kieliba et al., 2021; Wesselink et al., 2019). The canonical RDM was based on 7T finger movement fMRI data in an independently acquired cohort of healthy controls (n = 8). The S1 hand ROI used to calculated this canonical RDM was defined similarly as in the current study (see Wesselink and Maimon-Mor, (2017b) for details). Note that results were unchanged when calculating typicality scores using a canonical RDM based on the averaged RDM of the sex-, handedness-, and age matched control group tested in this study (see Appendix 1).”

Revised text Appendix 1:

“Typicality analysis using a canonical RDM based on the controls’ average RDM

To ensure that our typicality results did not change when using a canonical inter-finger RDM based on the age-, sex-, and handedness matched subjects tested in this study, we recalculated the typicality scores of all participants using the averaged inter-finger RDM of our control sample as the canonical RDM. We found a strong and highly significant correlation between the typicality scores calculated using the canonical inter-finger RDM from the independent dataset (reported in the main manuscript) and the typicality scores calculated using our controls’ average RDM. This was true for both the SCI patient (rs = 0.92, p < 0.001) and control groups (rs = 0.78, p < 0.001).

We then repeated all typicality analysis reported in the main manuscript. As expected, using the typicality scores calculated using our controls’ average RDM we found the same results as when using the canonical inter-finger RDM from the independent dataset: There was a significant difference in typicality between SCI patients, healthy controls, and congenital one-handers (H(2)=27.61, p < 0.001). We further found significantly higher typicality in controls compared to congenital one-handers (U=0, p < 0.001; BF10=76.11). Importantly, the typicality scores of the SCI patients were significantly higher than the congenital one-handers (U=2, p < 0.001; BF10=50.98), but not significantly different from the controls (U=94, p=0.24; BF10=0.55). Number of years since SCI significantly correlated with hand representation typicality (rs=-0.54, p=0.05) and patients with more retained GRASSP motor function of the tested upper limb had more typical hand representations in S1 (rs=0.58, p=0.03). There was no significant correlation between S1 hand representation typicality and GRASSP sensory function of the tested upper limb, spared midsagittal spinal tissue bridges at the lesion level, or cross-sectional spinal cord area (rs=0.40, p=0.15, rs=0.50, p=0.10, and rs=0.48, p=0.08, respectively). An exploratory stepwise linear regression analysis revealed that years since SCI significantly predicted hand representation typicality in S1 with R2=0.33 (F(1,10)=4.98, p=0.05). Motor function, sensory function, spared midsagittal spinal tissue bridges at the lesion level, and spinal cord area did not significantly add to the prediction (t=1.31, p=0.22, t=1.62, p=0.14, t=1.70, p=0.12, and t=1.09, p=0.30, respectively).”

• Methods & Results: The authors make a few unproven claims, such as saying "generally, the position, order of finger preference, and extent of the hand maps were qualitatively similar between patients and control". There are no data to support these claims.

As indicated in this sentence, this claim substantiated a qualitative inspection of the finger maps in Figure 2 and we indeed do not support this claim with quantitative analysis. We have therefore removed this sentence from the revised manuscript and instead say, as per the suggestion of reviewer 1, that overall, there were aspects of somatotopic finger selectivity in the SCI patients’ hand maps,

Revised text Results:

“Overall, we found aspects of somatotopic finger selectivity in the maps of SCI patients’ hands, in which neighbouring clusters showed selectivity for neighbouring fingers in contralateral S1, similar to those observed in eighteen age-, sex-, and handedness matched healthy controls (see Figure 2A&B). A characteristic hand map shows a gradient of finger preference, progressing from the thumb (red, laterally) to the little finger (pink, medially). Notably, a characteristic hand map was even found in a patient who suffered complete paralysis and sensory deprivation of the hands (Figure 2. patient map 1; patient S01). Despite most maps (Figure 2, except patient map 3) displaying aspects of characteristic finger selectivity, some finger representations were not visible in the thresholded patient and control maps.”

• Methods & Results: The authors argue that the map architecture is topographic as soon as the dissimilarity between two different fingers is above 0. First, what I am really wondering about is why the authors do not provide the exact dissimilarity values in the text but only give the stats for the difference to 0 (t-value, p-value, Bayes factor). Were the dissimilarity values perhaps very low? The values should be reported. Also, when this argument that maps are topographic as long as the value of two different fingers is above 0 should hold, then the authors have to show that the value for mapping the SAME finger is indeed 0. Otherwise, this argument is not convincing.

We would like to clarify that a representation is not per se topographic when the RSA dissimilarity is > 0. The dissimilarity value provided by RSA indicates the extent to which a pair of conditions is distinguished – it can be viewed as encapsulating the information content carried by the region (Kriegeskorte et al., 2008). Due to cross-validation across runs, the expected distance value would be zero (but can go below 0) if two conditions’ activity patterns are not statistically different from each other, and larger than zero if there is differentiation between the conditions (fingers’ activity patterns in the S1 hand area in our case; Kriegeskorte et al., 2008; Nili et al., 2014). The diagonal of the RDM reflect comparisons between the same fingers and therefore reflect distances between the exact same activity pattern in the same run and are thus 0 by definition (Kriegeskorte et al., 2008; Nili et al., 2014). This was also the case in our individual participant RDMs. Since this is not a meaningful value (a distance between 2 identical activity patterns will always be 0) we chose not to report this. We have clarified the meaning of the separability measure in the revised Methods section.

To investigate whether a representation is somatotopic, we have to take into account the full fine-grained inter-finger distance pattern. The full fine-grained inter-finger distance pattern is related to everyday use of our hand and has been shown to depict the invariant representational structure of fingers better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). To determine whether a participant’s inter-finger distance pattern is somatotopic one should associate it to a canonical RDM – which is done in the typicality analysis (see also our response to comment 2.6).

What can be done to demonstrate the validity of an ROI, is to run RSA on a control ROI where one would not expect to find activity that is distinguishable between finger conditions. Rather than comparing your separability measure against 0, one can then compare the separability of your ROI that is expected to contain this information to that of your control ROI. We created a cerebral spinal fluid (CSF) ROI, repeated our RSA analysis in this ROI, and then compared the separability of the CSF and S1 hand area ROIs. As expected, there was a significant difference between separability (or representation strength) in the S1 hand area and CSF ROIs for both controls (W=171, p < 0.001; BF10=4059) and patients (W=105, p < 0.00; BF10=279). This analysis has been added to the revised manuscript.

Individual participant separability values (i.e., distances averaged across fingers) are visualised in Figure 3D. Following the reviewer’s suggestion, we have included individual participant inter-finger distance plots for both the controls and SCI patients as Figure 3- Figure supplement 2 and Figure 3- figure supplement 3, respectively. The inter-finger distances for each finger pair and subject can be extracted from this. We feel this is more readily readable and interpretable than a table containing the 10 inter-finger distance scores for all 32 participants. These values have instead been made available online, together with our other data, on https://osf.io/e8u95/.

Revised text Methods:

“If there is no information in the ROI that can statistically distinguish between the finger conditions, then due to cross-validation the expected distance measure would be 0. If there is differentiation between the finger conditions, the separability would be larger than 0 (Nili et al., 2014). Note that this does not directly indicate that this region contains topographic information, but rather that this ROI contains information that can distinguish between the finger conditions. To further ensure that our S1 hand ROI was activated distinctly for different fingers, we created a cerebral spinal fluid (CSF) ROI that would not contain finger specific information. We then repeated our RSA analysis in this ROI and statistically compared the separability of the CSF and S1 hand area ROIs.”

Revised text Results:

“We found that inter-finger separability in the S1 hand area was greater than 0 for patients (t(13) = 9.83, p < 0.001; BF10 = 6.77e +4) and controls (t(17) = 11.70, p < 0.001; BF10 = 6.92e +6), indicating that the S1 hand area in both groups contained information about individuated finger representations. Furthermore, for both controls (W = 171, p < 0.001; BF10 = 4059) and patients (W = 105, p < 0.001; BF10 = 279) there was significant greater separability (or representation strength) in the S1 hand area than in a control cerebral spinal fluid ROI that would not be expected to contain finger specific information. We did not find a significant group difference in inter-finger separability of the S1 hand area (t(30) = 1.52, p = 0.14; BF10 = 0.81), with the BF showing anecdotal evidence in favour of the null hypothesis.”

• Discussion. The authors argue that spared midsagittal spinal tissue bridges are not necessary because they were not predictive of hand representation typicality. First, the measure of typicality is questionable and should not be used to make general claims about the importance of structural differences. Second, given there were only n=14 patients included, one may question generally whether predictive modelling can be done with these data. This statement should therefore be removed.

We would like to clarify that, like the reviewer, we do not believe that spared midsagittal spinal tissue bridges are unimportant. Indeed, a large body of our own research focuses on the importance of spared spinal tissue bridges in recovery of sensorimotor function and pain (Huber et al., 2017; Pfyffer et al., 2021, 2019; Vallotton et al., 2019). We have added a clarification sentence regarding the importance of tissue bridges with regards to recovery of function. We agree with the reviewer that given our limited sample size, it is difficult to make conclusive claims based on non-significant predictive modelling and correlational results. In the revised manuscript we therefore focus this statement (i.e., that sensory and motor hand function and tissue bridges are not necessary to preserve hand somatotopy) on our finding that two patients without spared tissue bridges at the lesion level and with complete or near complete loss of sensory and motor hand function had a highly typical hand representation. We present our predictive modelling results as being in line with this notion and added a word of caution that it is challenging to draw definite conclusions from non-significant predictive modelling and correlation results in such a limited sample size.

With regards to the reviewer’s concern about the validity of the typicality measure – please see our detailed response to comment 2.6.

Revised text Discussion:

“Spared spinal cord tissue bridges can be found in most patients with a clinically incomplete injury, their width being predictive of electrophysiological information flow, recovery of sensorimotor function, and neuropathic pain (Huber et al., 2017; Pfyffer et al., 2021, 2019; Vallotton et al., 2019). However, in this study, spared midsagittal spinal tissue bridges at the lesion level and sensorimotor hand function did not seem necessary to maintain and activate a somatotopic hand representation in S1. We found a highly typical hand representation in two patients (S01 and S03) who did not have any spared spinal tissue bridges at the lesion level, a complete (S01) or near complete (S03) hand paralysis, and a complete (S01) or near complete loss (S03) of hand sensory function. Our predictive modelling results were in line with this notion and showed that these behavioural and structural spinal cord determinants were not predictive of hand representation typicality. Note however that our sample size was limited, and it is challenging to draw definite conclusions from non-significant predictive modelling results.”

• Discussion. The authors say that hand representation is "preserved" in SCI patients. Perhaps it is better to be precise and to say that they active during movement planning.

We thank the reviewer for their suggestion and revised the Discussion accordingly.

Revised text Discussion:

"In this study we investigated whether hand somatotopy is preserved and can be activated through attempted movements following tetraplegia."

"How may these representations be preserved over time and activated through attempted movements in the absence of peripheral information?"

"Together, our findings indicate that in the first years after a tetraplegia, the somatotopic S1 hand representation is preserved and can be activated through attempted movements even in the absence of retained sensory function, motor function, and spared spinal tissue bridges."

Reviewer #3:

The demonstration that cortex associated with an amputated limb can be activated by other body parts after amputation has been interpreted as evidence that the deafferented cortex "reorganizes" and assumes a new function. However, other studies suggest that the somatotopic organization of somatosensory cortex in amputees is relatively spared, even when probed long after amputation. One possibility is that the stability is due to residual peripheral input. In this study, Kikkert et al. examine the somatotopic organization of somatosensory cortex in patients whose spinal cord injury has led to tetraplegia. They find that the somatotopic organization of the hand representation of somatosensory cortex is relatively spared in these patients. Surprisingly, the amount of spared sensorimotor function is a poor predictor of the stability of the patients' hand somatotopy. Nonethless, the hand representation deteriorates over decades after the injury. These findings contribute to a developing story on how sensory representations are formed and maintained and provide a counterpoint to extreme interpretations of the "reorganization" hypothesis mentioned above. Furthermore, the stability of body maps in somatosensory cortex after spinal cord injury has implications for the development of brain-machine interfaces.

I have only minor comments:

1) Given the controversy in the field, the use of the phrase "take over the deprived territory" (line 45) is muddled. Perhaps a more nuanced exposition of this phenomenon is in order?

We agree a more nuanced expression would be more appropriate. We have changed this sentence accordingly in the revised manuscript.

Revised text Introduction:

“Seminal research in nonhuman primate models of SCI has shown that this leads to extensive cortical reorganisation, such that tactile stimulation of cortically adjacent body parts (e.g. of the face) activated the deprived brain territory (e.g. of the hand; Halder et al., 2018; Jain et al., 2008; Kambi et al., 2014).”

2) The statement that "results are mixed" regarding intracortical microstimulation of S1 is dubious. In only one case has the hand representation been mislocalized, out of many cases (several at CalTech, 3 at the University of Pittsburgh, one at Case Western, one at Hopkins/APL, and one at UChicago). Perhaps rephrase to "with one exception?"

We agree that this sentence may give a wrong outlook on the literature and have changed the text per the reviewer’s suggestion.

Revised text Introduction:

“Case studies using intracortical stimulation in the S1 hand area to elicit finger sensations in SCI patients hint at such preserved somatotopic representations (Fifer et al., 2020; Flesher et al., 2016), with one exception (Armenta Salas et al., 2018).”

3) The phrase "tetraplegic sinal cord injury" seems awkward.

Thank you for highlighting this to us. We have corrected these instances in our revised manuscript to “tetraplegia”.

4) The stability of the representation is attributed to efference copy from M1. While this is a fine speculation, somatosensory cortex is part of a circuit and is interconnected with many other brain areas, M1 being one. Perhaps the stability is maintained due to the position of somatosensory cortex within this circuit, and not solely by its relationship with M1? There seems to be an overemphasis of this hypothesis at the exclusion of others.

Thank you for this comment. We agree we overemphasized the efference copy theory. We have adjusted this and now provide a more balanced description of potential circuits and interconnections that could maintain somatotopic representations after tetraplegia.

Author Response

Reviewer #1 (Public Review):

It is well established that valuation and value-based decision-making is context-dependent. This manuscript presents the results of six behavioral experiments specifically designed to disentangle two prominent functional forms of value normalization during reward learning: divisive normalization and range normalization. The behavioral and modeling results are clear and convincing, showing that key features of choice behavior in the current setting are incompatible with divisive normalization but are well predicted by a non-linear transformation of range-normalized values.

Overall, this is an excellent study with important implications for reinforcement learning and decision-making research. The manuscript could be strengthened by examining individual variability in value normalization, as outlined below.

We thank the Reviewer for the positive appreciation of our work and for the very relevant suggestions. Please find our point-by-point answer below.

There is a lot of individual variation in the choice data that may potentially be explained by individual differences in normalization strategies. It would be important to examine whether there are any subgroups of subjects whose behavior is better explained by a divisive vs. range normalization process. Alternatively, it may be possible to compute an index that captures how much a given subject displays behavior compatible with divisive vs. range normalization. Seeing the distribution of such an index could provide insights into individual differences in normalization strategies.

Thank you for pointing this out, it is indeed true that there is some variability. To address this, and in line with the Reviewer’s suggestion, we extracted model attributions per participant on the individual out-of-sample log-likelihood, using the VBA_toolbox in Matlab (Daunizeau et al., 2014). In experiment 1 (presented in the main text), we found that the RANGE model accounted for 79% of the participants, while the DIVISIVE model accounted for 12%. The relative difference was even higher when including the RANGEω model in the model space: the RANGE and RANGEω models account for a total of 85% of the participants, while the DIVISIVE model accounted only for 5%.

In experiment 2 (presented in the supplementary materials), the results were comparable (see Figure 3-figure supplement 3: 73% vs 10%, 83% vs 2%).

To provide further insights into the behavioral signatures behind inter-individual differences, we plotted the transfer choice rates for each group of participants (best explained by the RANGE, DIVISIVE, or UNBIASED models), and the results are similar to our model predictions from Figure 1C:

Author Response Image 1. Behavioral data in the transfer phase, split over participants best explained by the RANGE (left), DIVISIVE (middle) or UNBIASED (right) model in experiment 1 (A) and experiment 2 (B) (versions a, b and c were pooled together).

To keep things concise, we did not include this last figure in the revised manuscript, but it will be available for the interested readers in the Rebuttal letter.

One possibility currently not considered by the authors is that both forms of value normalization are at work at the same time. It would be interesting to see the results from a hybrid model. R1.2 Thank you for the suggestion, we fitted and simulated a hybrid model as a weighted sum between both forms of normalization:

First, the HYBRID model quantitatively wins over the DIVISIVE model (oosLLHYB vs oosLLDIV : t(149)=10.19, p<.0001, d=0.41) but not over the RANGE model, which produced a marginally higher log-likelihood (oosLLHYB vs oosLLRAN : t(149)=-1.82, p=.07, d=-0.008). Second, model simulations also suggest that the model would predict a very similar (if not worse) behavior compared to the RANGE model (see figure below). This is supported by the distribution of the weight parameter over our participants: it appears that, consistently with the model attributions presented above, most participants are best explained by a range-normalization rule (weight > 0.5, 87% of the participants, see figure below). Together, these results favor the RANGE model over the DIVISIVE model in our task.

Out of curiosity, we also implemented a hybrid model as a weighted sum between absolute (UNBIASED model) and relative (RANGE model) valuations:

Model fitting, simulations and comparisons slightly favored this hybrid model over the UNBIASED model (oosLLHYB vs oosLLUNB: t(149)=2.63, p=.0094, d=0.15), but also drastically favored the range normalization account (oosLLHYB vs oosLLRAN : t(149)=-3.80, p=.00021, d=-0.40, see Author Response Image 2).

Author Response Image 2. Model simulations in the transfer phase for the RANGE model (left) and the HYBRID model (middle) defined as a weighted sum between divisive and range forms of normalization (top) and between unbiased (no normalization) and range normalization (bottom). The HYBRID model features an additional weight parameter, whose distribution favors the range normalization rule (right).

To keep things concise, we did not include this last figure in the revised manuscript, but it will be available for the interested readers in the Rebuttal letter.

Reviewer #2 (Public Review):

This paper studies how relative values are encoded in a learning task, and how they are subsequently used to make a decision. This is a topic that integrates multiple disciplines (psych, neuro, economics) and has generated significant interest. The experimental setting is based on previous work from this research team that has advanced the field's understanding of value coding in learning tasks. These experiments are well-designed to distinguish some predictions of different accounts for value encoding. However there is an additional treatment that would provide an additional (strong) test of these theories: RN would make an equivalent set of predictions if the range were equivalently adjusted downward instead (for example by adding a "68" option to "50" and "86", and then comparing to WB and WT). The predictions of DN would differ however because adding a low-value alternative to the normalization would not change it much. Would the behaviour of subjects be symmetric for equivalent ranges, as RN predicts? If so this would be a compelling result, because symmetry is a very strong theoretical assumption in this setting.

We thank the Reviewer for the overall positive appraisal concerning our work, but also for the stimulating and constructive remarks that we have addressed below. At this stage, we just wanted to mention that we also agree with the Reviewer concerning the fact that a design where we add "68" option to "50" and "86" would represent also an important test of our hypotheses. This is why we had, in fact, run this experiment. Unfortunately, their results were somehow buried in the Supplementary Materials of our original submission and not correctly highlighted in the main text. We modified the manuscript in order to make them more visible:

Behavioral results in three experiments (N=50 each) featuring a slightly different design, where we added a mid value option (NT68) between NT50 and NT87 converge to the same broad conclusion: the behavioral pattern in the transfer phase is largely incompatible with that predicted by outcome divisive normalization during the learning phase (Figure 2-figure supplement 2).

Reviewer #3 (Public Review):

Bavard & Palminteri extend their research program by devising a task that enables them to disassociate two types of normalisation: range normalisation (by which outcomes are normalised by the min and max of the options) and divisive normalisation (in which outcomes are normalised by the average of the options in ones context). By providing 4 different training contexts in which the range of outcomes and number of options vary, they successfully show using 'ex ante' simulations that different learning approaches during training (unbiased, divisive, range) should lead to different patterns of choice in a subsequent probe phase during which all options from the training are paired with one another generating novel choice pairings. These patterns are somewhat subtle but are elegantly unpacked. They then fit participants' training choices to different learning models and test how well these models predict probe phase choices. They find evidence - both in terms of quantitive (i.e. comparing out-of-sample log-likelihood scores) and qualitative (comparing the pattern of choices observed to the pattern that would be observed under each mode) fit - for the range model. This fit is further improved by adding a power parameter which suggests that alongside being relativised via range normalisation, outcomes were also transformed non-linearly.

I thought this approach to address their research question was really successful and the methods and results were strong, credible, and robust (owing to the number of experiments conducted, the design used and combination of approaches used). I do not think the paper has any major weaknesses. The paper is very clear and well-written which aids interpretability.

This is an important topic for understanding, predicting, and improving behaviour in a range of domains potentially. The findings will be of interest to researchers in interdisciplinary fields such as neuroeconomics and behavioural economics as well as reinforcement learning and cognitive psychology.

We thank Prof. Garrett for his positive evaluation and supportive attitude.

Author Response

Reviewer #1 (Public Review):

In this paper, Fernandes et al. take advantage of synthetic constructs to test how Bicoid (Bcd) activates its downstream target Hunchback (Hb). They explore synthetic constructs containing only Bcd, Bcd and Hb, and Bcd and Zelda binding sites. They use these to develop theoretical models for how Bcd drives Hb in the early embryo. They show that Hb sites alone are insufficient to drive further Hb expression.

The paper's first half focuses on how well the synthetic constructs replicate the in vivo expression of hb. This approach is generally convincing, and the results are interesting. Consistent with previous work, they show that Bcd alone is sufficient to drive an expression profile that is similar to wild‐type, but the addition of Hb and Zelda are needed to generate precise and rapid formation of the boundaries. The experimental results are supported by modelling. The model does a nice job of encapsulating the key conclusions and clearly adds value to the analysis.

In the second part of the paper, the authors use their synthetic approach to look at how the Hb boundary alters depending on Bcd dosage. This part asks whether the observed Bcd gradient is the same as the activity gradient of Bcd (i.e. the "active" part of Bcd is not a priori the same as the protein gradient). This is a very interesting problem and good the authors have tried to tackle this. However, the strength of their conclusions needs to be substantially tempered as they rely on an overestimation of the Bcd gradient decay length.

Comments:

‐ My major concern regards the conclusions for the final section on the activity gradient. In the Introduction it is stated: "[the Bcd gradient has] an exponential AP gradient with a decay length of L ~ 20% egg‐length (EL)". While this was the initial estimate (Houchmandzadeh et al., Nature 2002), later measurements by the Gregor lab (see Supplementary Material of Liu et al., PNAS 2013) found that "The mean length constant was reduced to 16.5 ± 0.7%EL after corrections for EGFP maturation". The original measurements by Houchmandzadeh et al. had issues with background control, that also led to the longer measured decay length. In later work, Durrieu et al., Mol Sys Biol 2018, found a similar scale for the decay length to Liu et al. Looking at Figure 5, a value of 16.5%EL for the decay length is fully consistent with the activity and protein gradients for Bcd being similar. In short, the strength of the conclusions clearly does not match the known gradient and should be substantially toned down.

The reviewer is right: several studies aiming to quantitatively measure the Bicoid protein gradient ended‐up with quite different decay lengths.

A summary of the various decay lengths measured, and the method used for these measurements is given below:

As indicated, these measurements are quite variable among the different studies and the differences can potentially be attributed to different methods of detection (antibody staining on fixed samples vs fluorescent measurements on live sample) or to the type of protein detected (endogenous Bicoid vs fluorescently tagged).

We agree with the reviewer that given these discrepancies, the exact value of the Bcd protein gradient decay length is not known and that we only have measurements that put it in between 16 and 25 % EL (see the Table above). Therefore, we agree that we should tone down the difference between the protein vs activity gradient and focus on the measurements of the effective activity gradient decay length allowed by our synthetic reporters. This allows us to revisit the measurement of the Hill coefficient of the transcription step‐like response, which is based on the decay‐length for the Bcd protein gradient, and assumed in previous published work to be of 20% EL (Gregor et al., Cell, 2007a; Estrada et al., 2016; Tran et al., PLoS CB, 2018). Importantly, the new Hill coefficient allows us to set the Bcd system within the limits of an equilibrium model.

As mentioned by the reviewer, it is possible that the decay length of the protein gradient measured using antibody staining (Houchmandzadeh et al,, Nature, 2002) was not correct due to background controls. Such measurements were also performed in Xu et al. (2015) which agree with the original measurements (Houchmandzadeh et al., Nature 2002). As indicated in the table above, all the other measurements of the Bcd protein gradient decay length were done using fluorescently tagged Bcd proteins and we cannot exclude the possibility the wt vs tagged protein might have different decay lengths due to potentially different diffusion coefficients or half‐lives. Before drawing any conclusion on the exact value of the endogenous Bcd protein gradient decay length, it is essential to measure it again in conditions that correct for the background issues for immuno‐staining as it was done in Liu et al., PNAS, 2013 for the Bcd‐eGFP protein. In this study, the authors only measured the decay length of the Bcd fusion protein using immuno‐staining for the Bcd protein. Unfortunately, in this study, the authors did not measure again the decay length of the endogenous Bcd protein gradient using immuno‐staining and the same procedure for background control. Therefore, they do not firmly exclude the possibility that the endogenous vs tagged Bcd proteins might have different decay length.

We thank the reviewer for his comment which helped us to clarify the message. In addition, as there is clearly an issue for the measurements of the Bcd protein gradient, we added a section in the SI (Section E) and a Table (Table S4) describing the various decay length measured for the Bcd or the Bcd‐fluorescently tagged protein gradients from previous studies. In the discussion, together with the possibility that there might be a protein vs activity gradient (as we originally proposed and believe is still a valid possibility), we also discuss the alternative possibility proposed by the reviewer which is that the protein vs activity gradients have the same decay lengths but that the decay length of the Bcd protein gradient was potentially not correctly evaluated.

‐ All of the experiments are performed in a background with the hb gene present. Does this impact on the readout, as the synthetic lines are essentially competing with the wild‐type genes? What controls were done to account for this?

We agree with the reviewer that this concern might be particularly relevant at the hb boundary where a nucleus has been shown to only contain ~ 700 Bicoid molecules (Gregor et al., Cell, 2007b). However, ~1000 Bicoid binding regions have been identified by ChIP seq experiments in nc14 embryos (Hannon et al., Elife, 2017) and given that several Bcd binding sites are generally clustered together in a Bcd region, the number of Bcd binding sites in the fly genome is likely larger than 1000. It is much greater than the number of Bicoid binding sites in our synthetic reporters. Therefore, we think that it is unlikely that adding the synthetic reporters (which in the case of B12 only represents at most 1/100 of the Bcd binding sites in the genome) will severely alter the competition for Bcd binding between the other Bcd binding sites in the genome. Additionally, the insertion of a BAC spanning the endogenous hb locus with all its Bcd‐dependent enhancers did not affect (as far as we can tell) the regulation of the wildtype gene (Lucas, Tran et al., 2018).

We have added a sentence concerning this point in the main text (lines 108 to 111).

‐ Further, the activity of the synthetic reporters depends on the location of insertion. Erceg et al. PLoS Genetics 2014 showed that the same synthetic enhancer can have different readout depending on its genomic location. I'm aware that the authors use a landing site that appears to replicate similar hb kinetics, but did they try random insertion or other landing site? In short, how robust are their results to the specific local genome site? This should have been tested, especially given the boldly written conclusions from the work.

This concern of the reviewer has been tested and is addressed Fig S1 where we compare two random insertions of the hb‐P2 transgene (on chromosome II and III; Lucas, Tran et al., 2018) and the insertion at the VK33 landing site that was used for the whole study. As shown Fig. S1, the dynamics of transcription (kymographs) are very similar. In the main text, the reference Fig. S1 is found in the Materials and Methods section (bottom of the 1st paragraph concerning the Drosophila stocks, lines 518).

‐ Related to the above, it's also not obvious that readout is linear ‐ i.e. as more binding sites are added, there could be cooperativity between binding domains. This may have been accounted for in the model but it is not clear to me how.

The reviewer is totally correct. It is clear from our data that readout is not linear: comparing (increase of 1.5 X in the number of BS) B6 with B9 leads to a 4.5 X greater activation rate and this argues against independent activation of transcription by individual bound Bcd TF. There is almost no impact of adding 3 more sites when comparing B9 to B12 (even though it corresponds to an increase of 1.33 X in the number of BS). This issue has been rephrased in the main text (lines 200 to 203) and further developed for the modeling aspects in the SI section C and Figure S3. It is also discussed in the second paragraph of the discussion (lines 380 to 383).

‐ It would be good in the Introduction/Discussion to give a broader perspective on the advantages and disadvantages of the synthetic approach to study gene regulation. The intro only discusses Tran et al. Yet, there is a strong history of using this approach, which has also helped to reveal some of the approaches shortcoming. E.g. Gertz et al. Nature 2009 and Sharon et al. Nature Biotechnology 2012. Again, I may have missed, but from my reading I cannot see any critical analysis of the pros/cons of the synthetic approach in development. This is necessary to give readers a clearer context.

One sentence was added in the introduction concerning this point (lines 79 to 82).

A short review concerning the synthetic approach in development has also been added at the beginning of the discussion (lines 347 to 359).

Reviewer #2 (Public Review):

It is known that Bicoid increases in concentration across the syncytial division cycles, the gradient length scale for Bicoid does not change, and hunchback also increases in concentration during the syncytial cycles but the sharp boundary of the hunchback gradient is constantly seen despite the change in concentration of Bicoid. This manuscript shows that by increasing the Bicoid concentration or by adding Zelda binding sites, the expression of hunchback can be recapitulated to that of a previously studied promoter for hunchback.

I have the following comments to understand the implications of the study in the context of increasing concentrations of Bicoid during the syncytial division cycles:

‐ Bicoid itself is also increasing over the syncytial division cycles, how does this change in concentration of Bicoid affect the activation of the hunchback promoter given the cooperative binding of Bicoid and Bicoid and Zelda as documented by the study?

We thank the reviewer for this remark about the dynamics of the Bcd gradient, which we may have taken for granted. A seminal work on the dynamics of the Bcd gradient using fluorescent‐tagged Bcd (Gregor et al, Cell, 2007a) has shown that the gradient of Bcd nuclear concentration (this nuclear concentration is the one that matter for transcription) remains stable over nuclear cycles, despite a global increase of Bcd amount in the embryo. This can be explained by the fact that Bcd molecules are imported in the nuclei and that the number of nuclei double at every cycle, such that both processes compensate each other. Thus, we assumed that the gradient of Bcd nuclear concentration was stable over nc11 to nc13.

We have clarified this assumption in the model section in the manuscript (lines 165‐168).

Supporting our assumption, when looking at the transcription dynamics regulated by Bcd, in Lucas et al, PLoS Gen, 2018, we observed very reproducible expression pattern dynamics of the hb‐P2 reporter at each cycle nc11 to nc13. Such reproducibility in the pattern dynamics were also observed in this current work for hb‐P2, B6, B9, B12 and H6B6 reporters (Fig. S6A). Also, in Lucas et al, PLoS Gen, 2018, the shift in the established boundary positions of hb‐P2 reporter between nc11 to nc13 is ~2%EL (approximately a nucleus length ~10μm) and it is thus marginal.

In addition, as mentioned in the text (lines 105 to 107), we only focused our analysis on nc13 data which are statistically stronger given the higher number of nuclei analyzed. Thus, any change of Bcd nuclear concentration that would happen over nuclear cycles will not matter.

Concerning Zelda: Zelda’s transcriptional activity when measured on a reporter with only 6 Zld binding sites changes drastically over the nuclear cycles, with strong activity at nc11 and much weaker activity at nc13 (Fig S4A). This indicates that the changes in expression pattern dynamics of Z2B6 from nc11 to nc13 are caused predominantly by decreasing Zelda activity: the effect of Zld on the Z2B6 promoter is very strong during nc11 and nc12. It is also very strong at the beginning of nc13 (even though the Z6 reporter is almost silent) and became a bit weaker in the second part of nc13 (Fig S4B‐D).

‐ Does the change in concentration of Bicoid across the nuclear cycles shift the gradient similar to the change in numbers of Bicoid binding sites?

In both Lucas et al, PLoS Gen, 2018 and in this work (Fig. 1, Fig. 3 and Fig. S6A), we found that the positions of the expression boundary are very reproducible and stable in time for hb‐P2, B6, B9, B12, H6B6 during the interphase of nc12 to 13. For hb‐P2, the averaged shift of the established boundary position in nc11, 12 and 13 is within 2 %EL. This averaged shift between the cycles is of similar magnitude to the difference caused by embryo‐to‐embryo variability within nc13 (~2 %EL) (Gregor et al, Cell, 2007b, Lucas et al, PloS Gen, 2018). This shift is much smaller than the difference between the expression boundary positions of B6 and B9 (~ 8 % EL) and between B6 and Z2B6 (~17.5 %EL) in nc13.

For these reasons, we conclude that the difference between the expression patterns of B6, B9 and Z2B6 are caused predominantly by changing the TF binding site configurations of the reporters, rather than variability in the Bcd gradient.

The assumption of gradient stability has been clarified in the previous answer and in the manuscript (lines 165‐168).

‐ The intensity is a little higher for B9 and B12 at the anterior in 2B? Is this statistically different? is this likely to change the amount of Bicoid expression at the locus and lead to more robust activation?

We performed statistical tests to distinguish the spot intensities at the anterior pole for every pair of reporters in Fig. 2B (hb‐P2, B6, B9 and B12). All p‐values from pair‐wise KS tests are greater than 0.067, suggesting that the spot intensities at the anterior pole are not distinguishable between these reporters.

We have clarified this in the manuscript (line 157).

‐Are the fraction of active loci not changing across the syncytial cycles when the concentration of Bicoid also changes and consistent with the synthetic promoters?

To measure the reproducibility of the expression pattern dynamics in different nuclear cycles, we compared the boundary position of the fraction of active loci pattern as a function of time for all hbP2 and synthetic reporters (Fig. S6A). In this figure panel, for all reporters except Z2B6, the curves in nc12 and nc13 largely overlap, suggesting high reproducibility in the pattern dynamics between cycles and consequently low sensitivity to the subtle variation in the Bcd nuclear concentration gradient between the cycles.

For Z2B6, we attributed the difference in pattern dynamics between nc12 and nc13 to the changes in Zelda activity, as validated independently with a synthetic reporter with only 6 Zld binding sites (Fig. S4A).

‐How do the numbers of Hb BS change the expression of Hb? H6B6 has 6 Hb BS whereas the Hb‐P2 has 1? Are more controls needed to compare these 2 contexts?

As our goal was to determine to which mechanistic step of our model each TF (Bcd, Hb, Zld) contributed, we added BS numbers that are much higher than in the hb‐P2 promoter. The added number of Hb BS remains very low when compared to total number of Hb binding sites in the entire genome (Karplan et al, PLOS Gen, 2011), therefore, it is very unlikely to affect the endogenous expression of Hb protein.

We clarified this in the manuscript (lines 211 to 212).

Does Zelda concentration change across the syncytial division cycles? How does the change in concentration in the natural context affect the promoter activation of Hb?

Zelda concentration is stable over the nuclear cycles, as observed with the fluorescently‐tagged Zld protein (Dufourt et al., Nat Com, 2018). However, Zelda’s transcriptional activity when measured on a reporter with only 6 Zld binding sites changes drastically over the nuclear cycles, with strong activity at nc11 and much weaker activity at nc13 (Fig S4A, this work).

The impact of this change in Zld activity can be observed with the Z2B6 promoter, with the expression boundary moving from the posterior region toward the anterior region over the nuclear cycles (Fig. S4B‐D). However, we don’t detect any changes in the expression pattern dynamics of hb‐P2 over the nuclear cycles (Fig. S6A and in Lucas et al., PLoS Gen, 2018).

We have clarified this in lines 250‐251 of the main manuscript.

‐Changing the dose of Bicoid shifts the boundary of hunchback expression. It would be nice to model or test this in the context of varing doses of zelda or even reason this with respect to varying doses of zelda across the syncytial division cycles.

We thank the reviewer for this insight. Concerning Zelda, we did not perform any experiment reducing the amount of Zelda in the embryo. However, in a previous study (Lucas et al., PLoS Genetics, 2018), we observed that the boundary of hb was shifted towards the anterior when decreasing the amount of Zelda consistent to the fact that the dose of Zelda is critical to set the boundary position and the threshold of Bcd concentration required for activation. However, as Zelda is distributed homogeneously along the AP axis, it cannot bring per se positional information to the system.

Reviewer #3 (Public Review):

I think the framing could be improved to better reflect the contribution of the work. From the abstract, for example, it's unclear to me what the authors think is the most meaningful conclusion. Is it the observations about the finer details of TF regulation (bursting dynamics), the fact that Bcd is probably the sole source of "positional information" for hb‐p2, that Bcd exists in active/inactive form, or the fact that an equilibrium model probably suffices to explain what we observe? The first sentence itself seems to suggest this paper will discuss "dynamic positional information", in which case it's somewhat misleading to say this kind of work is "largely unexplored"; Johannes Jaeger in particular has been a strong proponent of this view since at least 2004. On that note some particularly relevant recent papers in the Drosophila early embryo include:

1) Jaeger and Verd (2020) Curr Topics Dev Biol

2) Verd et al. (2017) PLoS Comp Biol

3) Huang, Amourda, et al. and Saunders (2017) eLife

4) Yang, Zhu, et al. (2020) eLife [see also the second half of Perkins (2021) PLoS Comp Biol for further discussion of that model]

‐Some reviews from James Briscoe also discuss this perspective.

We agree with the reviewer that the phrasing of the abstract was not clear enough to emphasize the contribution of the work and we are also sorry if it suggested that the dynamic positional information is largely unexplored because this was not at all our intention.

We rephrased the abstract aiming to better highlight the most meaningful conclusions.

‐I would also recommend modifying the title to reflect the biology found in the new results.

We modified the title to better reflect the new results:<br /> “Synthetic reconstruction of the hunchback promoter specifies the role of Bicoid, Zelda and Hunchback in the dynamics of its transcription”

‐A major point that the authors should address is the design of the synthetic constructs. From table S1, the sites are often very closely linked (4‐7 base pairs). From the footprint of these proteins, we know they can cover DNA across this size (see, https://pubmed.ncbi.nlm.nih.gov/8620846/). As such, there may be direct competition/steric hindrance (see https://pubmed.ncbi.nlm.nih.gov/28052257/). What impact does this have on their interpretations? Note also that the native enhancer has spaced sites with variable identities.

We completely agree with the reviewer comment in the sense that we named our reporters according to the number (N) of Bcd binding sites sequences that they contain, even though we cannot prove definitively that they can effectively be bound simultaneously by N Bcd molecules. It is thus possible that B9 is not a B9 but an effective B6 (i.e. B9 can only be bound simultaneously by 6 molecules) if, for instance, the binding of a Bcd molecule to one site would prevent by the binding of another Bcd molecule to a nearby site (as proposed by the reviewer in the case of direct competition or steric hindrance).

Even though we cannot exclude this possibility, we think that our use of B6, B9, B12, in reference to the 6 Bcd BS of hb‐P2 promoter, is relevant for several reasons : i) some of the Bcd BS in the hb‐P2 promoter are also very close from each other (see Table S1); ii) the design of the synthetic construct was made by multimerizing a series of 3 strong Bcd binding sites with a similar spacing as found for the closest sites in the hb‐P2 promoter (as shown in Figure 1A and Table S1); iii) the binding of the Bicoid protein has been shown in foot printing experiments in vitro to be more efficient on sites of the hb‐P2 promoter that are close from each other, and this has even been interpreted as binding cooperativity (Ma et al., 1996); iv) even though these experiments were not performed with full‐length proteins, two molecules of the paired homeodomain (from the same family of DNA binding domain as Bcd) are able to simultaneously bind to two binding sites separated by only 2 base pairs. This binding to very close sites is even cooperative while when the two sites are distant by 5 base pairs or more, the simultaneous binding to the two sites occurs without cooperativity (Wilson et al., 1993).

Conversely, as it is very difficult to demonstrate that 9 Bcd molecules can effectively bind to our B9 promoter, it is very difficult to know exactly how many binding sites for Bcd the hb‐P2 contains, and a large debate concerning not only the number but also the identity of the Bcd sites in the hb promoter is still ongoing (Park et al., 2019; Ling et al., 2019).

As we cannot exclude the possibility that B9 is an effective B6, it remains possible that B9 and hb‐P2 (which is supposed to only contains 6 sites) have the same number of effective Bcd binding site and this could explain why the two reporters have very similar transcription dynamics and features.

Regarding other interpretations in the manuscript, we identified two other aspects that will be affected if our synthetic reporters have fewer effective sites than the number of sites they carry. The first one concerns the synergy, as the increase in the number of sites of 1.5 from B6 to B9 might be over‐estimated but this would even increase the synergistic effect given the 4.5 difference in activity of the two reporters (Fig. S3). The second one concerns the discussion on the Hill coefficient and the decay length where the effective number of binding sites (N) is required to determine the limit of concentration sensing (Fig. 5). This would particularly be important for the hb‐P2 promoter.

Except for these specific points, we don’t think that the possibility that reporters do not exactly contain as many as effective binding sites than proposed, has a huge impact on our interpretations and the general message conveyed in this manuscript. Most importantly, it is very clear that our B6 and B9 reporters differ only by three Bcd binding sites and have yet very distinct expression dynamics: while B9 recapitulates almost all transcription features of hb‐P2, B6 is far from achieving it. Similarly, H6B6 and Z2B6 have very different transcription features than B6 and these differences have been key for understanding the mechanistic functions of the three TF we studied.

This discussion has been added to the discussion (lines 400 to 414)

Author Response

Reviewer #1 (Public Review):

Overall, the science is sound and interesting, and the results are clearly presented. However, the paper falls in-between describing a novel method and studying biology. As a consequence, it is a bit difficult to grasp the general flow, central story and focus point. The study does uncover several interesting phenomena, but none are really studied in much detail and the novel biological insight is therefore a bit limited and lost in the abundance of observations. Several interesting novel interactions are uncovered, in particular for the SPS sensor and GAPDH paralogs, but these are not followed up on in much detail. The same can be said for the more general observations, eg the fact that different types of mutations (missense vs nonsense) in different types of genes (essential vs non-essential, housekeeping vs. stress-regulated...) cause different effects.

This is not to say that the paper has no merit - far from it even. But, in its current form, it is a bit chaotic. Maybe there is simply too much in the paper? To me, it would already help if the authors would explicitly state that the paper is a "methods" paper that describes a novel technique for studying the effects of mutations on protein abundance, and then goes on to demonstrate the possibilities of the technology by giving a few examples of the phenomena that can be studied. The discussion section ends in this way, but it may be helpful if this was moved to the end of the introduction.

We modified the manuscript as suggested.

Reviewer #2 (Public Review):

Schubert et al. describe a new pooled screening strategy that combines protein abundance measurements of 11 proteins determined via FACS with genome-wide mutagenesis of stop codons and missense mutations (achieved via a base editor) in yeast. The method allows to identify genetic perturbations that affect steady state protein levels (vs transcript abundance), and in this way define regulators of protein abundance. The authors find that perturbation of essential genes more often alters protein abundance than of nonessential genes and proteins with core cellular functions more often decrease in abundance in response to genetic perturbations than stress proteins. Genes whose knockouts affected the level of several of the 11 proteins were enriched in protein biosynthetic processes while genes whose knockouts affected specific proteins were enriched for functions in transcriptional regulation. The authors also leverage the dataset to confirm known and identify new regulatory relationships, such as a link between the SDS amino acid sensor and the stress response gene Yhb1 or between Ras/PKA signalling and GAPDH isoenzymes Tdh1, 2, and 3. In addition, the paper contains a section on benchmarking of the base editor in yeast, where it has not been used before.

Strengths and weaknesses of the paper

The authors establish the BE3 base editor as a screening tool in S. cerevisiae and very thoroughly benchmark its functionality for single edits and in different screening formats (fitness and FACS screening). This will be very beneficial for the yeast community.

The strategy established here allows measuring the effect of genetic perturbations on protein abundances in highly complex libraries. This complements capabilities for measuring effects of genetic perturbations on transcript levels, which is important as for some proteins mRNA and protein levels do not correlate well. The ability to measure proteins directly therefore promises to close an important gap in determining all their regulatory inputs. The strategy is furthermore broadly applicable beyond the current study. All experimental procedures are very well described and plasmids and scripts are openly shared, maximizing utility for the community.

There is a good balance between global analyses aimed at characterizing properties of the regulatory network and more detailed analyses of interesting new regulatory relationships. Some of the key conclusions are further supported by additional experimental evidence, which includes re-making specific mutations and confirming their effects on protein levels by mass spectrometry.

The conclusions of the paper are mostly well supported, but I am missing some analyses on reproducibility and potential confounders and some of the data analysis steps should be clarified.

The paper starts on the premise that measuring protein levels will identify regulators and regulatory principles that would not be found by measuring transcripts, but since the findings are not discussed in light of studies looking at mRNA levels it is unclear how the current study extends knowledge regarding the regulatory inputs of each protein.

See response to Comment #10.

Specific comments regarding data analysis, reproducibility, confounders

1) The authors use the number of unique barcodes per guide RNA rather than barcode counts to determine fold-changes. For reliable fold changes the number of unique barcodes per gRNA should then ideally be in the 100s for each guide, is that the case? It would also be important to show the distribution of the number of barcodes per gRNA and their abundances determined from read counts. I could imagine that if the distribution of barcodes per gRNA or the abundance of these barcodes is highly skewed (particularly if there are many barcodes with only few reads) that could lead to spurious differences in unique barcode number between the high and low fluorescence pool. I imagine some skew is present as is normal in pooled library experiments. The fold-changes in the control pools could show whether spurious differences are a problem, but it is not clear to me if and how these controls are used in the protein screen.

Because of the large number of screens performed in this study (11 proteins, with 8 replicates for each) we had to trade off sequencing depth and power against cell sorting time and sequencing cost, resulting in lower read and barcode numbers than what might be ideally aimed for. As described further in the response to Comment #5, we added a new figure to the manuscript that shows that the correlation of fold-changes between replicates is high (Figure 3–S1A). The second figure below shows that the correlation between the number of unique barcodes and the number of reads per gRNA is highly significant (p < 2.2e-16).

2) I like the idea of using an additional barcode (plasmid barcode) to distinguish between different cells with the same gRNA - this would directly allow to assess variability and serve as a sort of replicate within replicate. However, this information is not leveraged in the analysis. It would be nice to see an analysis of how well the different plasmid barcodes tagging the same gRNA agree (for fitness and protein abundance), to show how reproducible and reliable the findings are.

We agree with the reviewer that this would be nice to do in principle, but our sequencing depth for the sorted cell populations was not high enough to compare the same barcode across the low/unsorted/high samples. See also our response to Comment #5 for the replicate analyses.

3) From Fig 1 and previous research on base editors it is clear that mutation outcomes are often heterogeneous for the same gRNA and comprise a substantial fraction of wild-type alleles, alleles where only part of the Cs in the target window or where Cs outside the target window are edited, and non C-to-T edits. How does this reflect on the variability of phenotypic measurements, given that any barcode represents a genetically heterogeneous population of cells rather than a specific genotype? This would be important information for anyone planning to use the base editor in future.

We agree with the reviewer that the heterogeneity of editing outcomes is an important point to keep in mind when working with base editors. In genetic screens, like the ones described here, often the individual edit is less important, and the overall effects of the base editor are specific/localized enough to obtain insights into the effects of mutations in the area where the gRNA targets the genome. For example, in our test screens for Canavanine resistance and fitness effects, in which we used gRNAs predicted to introduce stop codons into the CAN1 gene and into essential genes, respectively, we see the expected loss-of-function effect for a majority of the gRNAs (canavanine screen: expected effect for 67% of all gRNAs introducing stop codons into CAN1; fitness screen: expected effect for 59% of all gRNAs introducing stop codons into essential genes) (Figure 2). In the canavanine screen, we also see that gRNAs predicted to introduce missense mutations at highly conserved residues are more likely to lead to a loss-of-function effect than gRNAs predicted to introduce missense mutations at less conserved residues, further highlighting the differentiated results that can be obtained with the base editor despite the heterogeneity in editing outcomes overall. We would certainly advise anyone to confirm by sequencing the base edits in individual mutants whenever a precise mutation is desired, as we did in this study when following up on selected findings with individual mutants.

4) How common are additional mutations in the genome of these cells and could they confound the measured effects? I can think of several sources of additional mutations, such as off-target editing, edits outside the target window, or when 2 gRNA plasmids are present in the same cell (both target windows obtain edits). Could some of these events explain the discrepancy in phenotype for two gRNAs that should make the same mutation (Fig S4)? Even though BE3 has been described in mammalian cells, an off-target analysis would be desirable as there can be substantial differences in off-target behavior between cell types and organisms.

Generally, we are not very concerned about random off-target activity of the base editor because we would not expect this to cause a consistent signal that would be picked up in our screen as a significant effect of a particular gRNA. Reproducible off-target editing with a specific gRNA at a site other than the intended target site would be problematic, though. We limited the chance of this happening by not using gRNAs that may target similar sequences to the intended target site in the genome. Specifically, we excluded gRNAs that have more than one target in the genome when the 12 nucleotides in the seed region (directly upstream of the PAM site) are considered (DiCarlo et al., Nucleic Acids Research, 2013).

We do observe some off-target editing right outside the target window, but generally at much lower frequency than the on-target editing in the target window (Figure 1B and Figure 1–S2). Since for most of our analyses we grouped perturbations per gene, such off-target edits should not affect our findings. In addition, we validated key findings with independent experiments. For our study, we used the Base Editor v3 (Komor et al., Nature, 2016); more recently, additional base editors have been developed that show improved accuracy and efficiency, and we would recommend these base editors when starting a new study (see, e.g., Anzalone et al., Nature Biotechnology, 2020).

We are not concerned about cases in which one cell gets two gRNAs, since the chance that the same two gRNAs end up in one cell repeatedly is low, and such events would therefore not result in a significant signal in our screens.

We don’t think that off-target mutations can explain the discrepancy between pairs of gRNAs that should introduce the same mutation (Figure 3–S1. The effect of the two gRNAs is actually well-correlated, but, often, one of the two gRNAs doesn’t pass our significance cut-off or simply doesn’t edit efficiently (i.e., most discrepancies arise from false negatives rather than false positives). We may therefore miss the effects of some mutations, but we are unlikely to draw erroneous conclusions from significant signals.

5) In the protein screen normalization uses the total unique barcode counts. Does this efficiently correct for differences from sequencing (rather than total read counts or other methods)? It would be nice to see some replicate plots for the analysis of the fitness as well as the protein screen to be able to judge that.

We made a new figure that shows a replicate comparison for the protein screen (see below; in the manuscript it is Figure 3–S1A) and commented on it in the manuscript. For this analysis, the eight replicates for each protein were split into two groups of four replicates each and analyzed the same way as the eight replicates. The correlation between the two groups of replicates is highly significant (p < 2.2e-16). The second figure shows that the total number of reads and the total number of unique barcodes are well correlated.

For the fitness screen, we used read counts rather than barcode counts for the analysis since read counts better reflect the dropout of cells due to reduced fitness. The figure below shows a replicate comparison for the fitness screen. For this analysis, the four replicates were split into two groups of two replicates each and analyzed the same way as the four replicates. The correlation between the two groups of replicates is highly significant (p < 2.2e-16).

6) In the main text the authors mention very high agreement between gRNAs introducing the same mutation but this is only based on 20 or so gRNA pairs; for many more pairs that introduce the same mutation only one reaches significance, and the correlation in their effects is lower (Fig S4). It would be better to reflect this in the text directly rather than exclusively in the supplementary information.

We clarified this in the manuscript main text: “For 78 of these gRNA pairs, at least one gRNA had a significant effect (FDR < 0.05) on at least one of the eleven proteins; their effects were highly correlated (Pearson’s R2 = 0.43, p < 2.2E-16) (Figure 3–S1B). For the 20 gRNA pairs for which both gRNAs had a significant effect, the correlation was even higher (Pearson’s R2 = 0.819, p = 8.8e-13) (Figure 3–S1C). These findings show that the significant gRNA effects that we identify have a low false positive rate, but they also suggest that many real gRNA effects are not detected in the screen due to limitations in statistical power.”

7) When the different gRNAs for a targeted gene are combined, instead of using an averaged measure of their effects the authors use the largest fold-change. This seems not ideal to me as it is sensitive to outliers (experimental error or background mutations present in that strain).

We agree that the method we used is more sensitive to outliers than averaging per gene. However, because many gRNAs have no effect either because they are not editing efficiently or because the edit doesn’t have a phenotypic consequence, an averaging method across all gRNAs targeting the same gene would be too conservative and not properly capture the effect of a perturbation of that gene.

8) Phenotyping is performed directly after editing, when the base editor is still present in the cells and could still interact with target sites. I could imagine this could lead to reduced levels of the proteins targeted for mutagenesis as it could act like a CRISPRi transcriptional roadblock. Could this enhance some of the effects or alter them in case of some missense mutations?

To reduce potential “CRISPRi-like” effects of the base editor on gene expression, we placed the base editor under a galactose-inducible promoter. For both the fitness and protein screens we grew the cultures in media without galactose for another 24 hours (fitness screen) or 8-9 hours (protein screens) before sampling. In the latter case, this recovery time corresponded to more than three cell divisions, after which we assume base editor levels to have strongly decreased, and therefore to no longer interfere with transcription. This is also supported by our ability to detect discordant effects of gRNAs targeting the same gene (e.g., the two mutations leading to loss-of-function and gain-of-function of RAS2), which would otherwise be overshadowed by a CRISPRi effect.

9) I feel that the main text does not reflect the actual editing efficiency very well (the main numbers I noticed were 95% C to T conversion and 89% of these occurring in a specific window). More informative for interpreting the results would be to know what fraction of the alleles show an edit (vs wild-type) and how many show the 'complete' edit (as the authors assume 100% of the genotypes generated by a gRNA to be conversion of all Cs to Ts in the target window). It would be important to state in the main text how variable this is for different gRNAs and what the typical purity of editing outcomes is.

We now show the editing efficiency and purity in a new figure (Figure 1B), and discuss it in the main text as follows: “We found that the target window and mutagenesis pattern are very similar to those described in human cells: 95% of edits are C-to-T transitions, and 89% of these occurred in a five-nucleotide window 13 to 17 base pairs upstream of the PAM sequence (Figure 1A; Figure 1–S2) (Komor et al., 2016). Editing efficiency was variable across the eight gRNAs and ranged from 4% to 64% if considering only cases where all Cs in the window are edited; percentages are higher if incomplete edits are considered, too (Figure 1B).”

Comments regarding findings

10) It would be nice to see a comparison of the results to the effects of ~1500 yeast gene knockouts on cellular transcriptomes (https://doi.org/10.1016/j.cell.2014.02.054). This would show where the current study extends established knowledge regarding the regulatory inputs of each protein and highlight the importance of directly measuring protein levels. This would be particularly interesting for proteins whose abundance cannot be predicted well from mRNA abundance.

We agree with the reviewer that it would be very interesting to compare the effect of perturbations on mRNA vs protein levels. We have compared our protein-level data to mRNA-level data from Kemmeren and colleagues (Kemmeren et al., Cell 2014), and we find very good agreement between the effects of gene perturbations on mRNA and protein levels when considering only genes with q < 0.05 and Log2FC > 0.5 in both studies (Pearson’s R = 0.79, p < 5.3e-15).

Gene perturbations with effects detected only on mRNA but not protein levels are enriched in genes with a role in “chromatin organization” (FDR = 0.01; as a background for the analysis, only the 1098 genes covered in both studies were considered). This suggests that perturbations of genes involved in chromatin organization tend to affect mRNA levels but are then buffered and do not lead to altered protein levels. There was no enrichment of functional annotations among gene perturbations with effects on protein levels but not mRNA levels.

We did not include these results in the manuscript because there are some limitations to the conclusions that can be drawn from these comparisons, including that our study has a relatively high number of false negatives, and that the genes perturbed in the Kemmeren et al. study were selected to play a role in gene regulation, meaning that differences in mRNA-vs-protein effects of perturbations are limited to this function, and other gene functions cannot be assessed.

11) The finding that genes that affect only one or two proteins are enriched for roles in transcriptional regulation could be a consequence of 'only' looking at 10 proteins rather than a globally valid conclusion. Particularly as the 10 proteins were selected for diverse functions that are subject to distinct regulatory cascades. ('only' because I appreciate this was a lot of work.)

We agree with this, and we think it is clear in the abstract and the main text of the manuscript that here we studied 11 proteins. We made this point also more explicit in the discussion, so that it is clear for readers that the findings are based on the 11 proteins and may not extrapolate to the entire yeast proteome.

Reviewer #3 (Public Review):

This manuscript presents two main contributions. First, the authors modified a CRISPR base editing system for use in an important model organism: budding yeast. Second, they demonstrate the utility of this system by using it to conduct an extremely high throughput study the effects of mutation on protein abundance. This study confirms known protein regulatory relationships and detects several important new ones. It also reveals trends in the type of mutations that influence protein abundances. Overall, the findings are of high significance and the method appears to be extremely useful. I found the conclusions to be justified by the data.

One potential weakness is that some of the methods are not described in main body of the paper, so the reader has to really dive into the methods section to understand particular aspects of the study, for example, how the fitness competition was conducted.

We expanded the first section for better readability.

Another potential weakness is the comparison of this study (of protein abundances) to previous studies (of transcript abundances) was a little cursory, and left some open questions. For example, is it remarkable that the mutations affecting protein abundance are predominantly in genes involved in translation rather than transcription, or is this an expected result of a study focusing on protein levels?

We thank the reviewer for pointing out that this paragraph requires more explanation. We expanded it as follows: “Of these 29 genes, 21 (72%) have roles in protein translation—more specifically, in ribosome biogenesis and tRNA metabolism (FDR < 8.0e-4, Figure 5C). In contrast, perturbations that affect the abundance of only one or two of the eleven proteins mostly occur in genes with roles in transcription (e.g., GO:0006351, FDR < 1.3e-5). Protein biosynthesis entails both transcription and translation, and these results suggest that perturbations of translational machinery alter protein abundance broadly, while perturbations of transcriptional machinery can tune the abundance of individual proteins. Thus, genes with post-transcriptional functions are more likely to appear as hubs in protein regulatory networks, whereas genes with transcriptional functions are likely to show fewer connections.”

Overall, the strengths of this study far outweigh these weaknesses. This manuscript represents a very large amount of work and demonstrates important new insights into protein regulatory networks.

Author Response

Reviewer #2 (Public Review):

The authors seek to determine how various species combine their effects on the growth of a species of interest when part of the same community.

To this end, the authors carry out an impressive experiment containing what I believe must be one of the largest pairwise + third-order co-culture experiments done to date, using a high-throughput co-culture system they had co-developed in previous work. The unprecedented nature of this data is a major strength of the paper. The authors also discover that species combine their effect through "dominance", i.e. the strongest effect masks the others. This is important as it calls into question the common assumption of additivity that is implicit in the choice of using Lotka-Volterra models.

A stronger claim (i.e. in the abstract) is that joint effect of multiple species on the growth of another can be derived from the effect of individual species. Unless I am misunderstanding something, this statement may have to be qualified a little, as the authors show that a model based on pairwise dominance (i.e. the strongest pairwise) does a somewhat better job (lower RMSD, though granted, not by much, 0.57 vs 0.63) than a model based on single species dominance. This is, the effect of the strongest pair predicts better the effect of a trio than the effect of the larger species.

This issue makes one wonder whether, had the authors included higher-order combinations of species (i.e. five-member consortia or higher), the strongest-effect trio would have predicted better than the strongest-effect pair, which in turn is better predictor than the strongest-effect species. This is important, as it would help one determine to what extent the strongest-effect model would work in more diverse communities, such as those one typically finds in nature. Indeed, the authors find that the predictive ability of the strongest effect species is much stronger for pairs than it is for trios (RMSD of 0.28 vs 0.63). Does the predictive ability of the single species model decline faster and faster as diversity grows beyond 4-member consortia?

Thank you for raising this important point. It is true that in our study we see that single species predict pairs better than trios, and that pairs predict trios better than single species. As we did not perform experiments on more diverse communities (n>4), we are not sure if or how these rules will scale up. We explicitly address these caveats in our revised discussion.

Reviewer #3 (Public Review):

A problem in synthetic ecology is that one can't brute-force complex community design because combinatorics make it basically impossible to screen all possible communities from a bank of possible species. Therefore, we need a way to predict phenomena in complex communities from phenomena in simple communities. This paper aims to improve this predictive ability by comparing a few different simple models applied to a large dataset obtained with the use of the author's "kchip" microfluidics device. The main question they ask is whether the effect of two species on a focal species is predicted from the mean, the sum, or the max of the effect of each single "affecting" species on the focal species. They find that the max effect is often the best predictor, in the sense of minimizing the difference between predicted effect and measured effect. They also measure single-species trait data for their library of strains, including resource niche and antibiotic resistance, and then find that Pearson correlations between distance calculations generated from these metrics and the effect of added species are weak and unpredictive. This work is largely well-done, timely and likely to be of high interest to the field, as predicting ecosystem traits from species traits is a major research aim.

My main criticism is that the main take-home from the paper (fig 3B)-that the strongest effect is the best predictor-is oversold. While it is true that, averaged over their six focal species, the "strongest effect" was the best overall predictor, when one looks at the species-specific data (S9), we see that it is not the best predictor for 1/3 of their focal species, and this fraction grows to 1/2 if one considers a difference in nRMSE of 0.01 to be negligible.

As suggested, we have softened our language regarding the take-home message. This matter is addressed in detail above in response to 'Essential Revisions'. Briefly, we see that the strongest model works best when both single species have qualitatively similar effects, but is slightly less accurate when effects are mixed. We also see overall less accurate predictions for positive effects. In light of these findings, we propose that focal species for which the strongest model is not the most accurate is due to the interaction types, and not specific to the focal species.

We made substantial changes to the manuscript, including the first paragraph of the discussion which more accurately describes these findings and emphasizes the relevant caveats:

"By measuring thousands of simplified microbial communities, we quantified the effects of single species, pairs, and trios on multiple focal species. The most accurate model, overall and specifically when both single species effects were negative, was the strongest effect model. This is in stark contrast to models often used in antibiotic compound combinations, despite most effects being negative, where additivity is often the default model (Bollenbach 2015). The additive model performed well for mixed effects (i.e. one negative and one positive), but only slightly better than the strongest model, and poorly when both species had effects of the same sign. When both single species’ effects were positive, the strongest model was also the best, though the difference was less pronounced and all models performed worse for these interactions. This may be due to the small effect size seen with positive effects, as when we limited negative and mixed effects to a similar range of effects strength, their accuracy dropped to similar values (Figure 3–Figure supplement 5). We posit that the difference in accuracy across species is affected mainly by the effect type dominating different focal species' interactions, rather than by inherent species traits (Figure 3–Figure supplement 6)." (Lines 288-304)

The same criticism applies to the result from figure 2-that pairs of affecting species have more negative effects than single species. Considered across all focal species this is true (though minor in effect size, Fig 2A). But there is only a significant effect within two individual species. Again, this points to the effects being focal-species-specific, and perhaps not as generalizable as is currently being claimed.

Upon more rigorous analysis, and with regard to changes in the dataset after filtering, we see that the more accurate statement is that effects become stronger, not necessarily more negative (in line with the accuracy of the strongest model). The overall trend is towards more negative interactions, due to the majority of interactions being negative, but as stated this is not true for each individual focal. As such the following sentence in the manuscript has been changed:

"The median effect on each focal was more negative by 0.28 on average, though the difference was not significant in all cases; additionally, focals with mostly positive single species interactions showed a small increase in median effect (Fig. 2D)" (Lines 151-154)

As well as the title of this section: "Joint effects of species pairs tend to be stronger than those of individual affecting species" (Lines 127-128)

Another thing that points to a focal-species-specific response is Fig 2D, which shows the distributions of responses of each focal species to pairs. Two of these distributions are unimodal, one appears bimodal, and three appear tri-modal. This suggests to me that the focal species respond in categorically different ways to species addition.

We believe this distribution of pair effects is related to the distribution of single species effects, and not to the way in which different focal species respond to the addition of second species. Though this may be difficult to see from the swarm plots shown in the paper, below is a split violin plot that emphasizes this point.

Fig R1: Distribution of single species and pair effects. Distribution of the effect of single and pairs of affecting species for each focal species individually. Dashed lines represent the median, while dotted lines the interquartile range.

These differences occur even though the focal bacteria are all from the same family. This suggests to me that the generalizability may be even less when a more phylogenetically dispersed set of focal species are used.

We have added the following sentence to the discussion explicitly emphasizing the phylogenetic limitations of our study:

"Lastly, it is important to note that our focal species are all from the same order (Enterobacterales), which may also limit the purview of our findings." (Lines 364-366)

Considering these points together, I argue that the conclusion should be shifted from "strongest effect is the best" to "in 3 of our focal species, strongest effect was the best, but this was not universal, and with only 6 focal species, we can't know if it will always be the best across a set of focal species".

As mentioned above, we have softened our language regarding the take-home message in response to these evaluations.

My second main criticism is that it is hard to understand exactly how the trait data were used to predict effects. It seems like it was just pearson correlation coefficients between interspecies niche distances (or antibiotic distances) and the effect. I'm not very surprised these correlations were unpredictive, because the underlying measurements don't seem to be relevant to the environment tested. What if, rather than using niche data across 20 nutrients, only the growth data on glucose (the carbon source in the experiments) was used? I understand that in a field experiment, for example, one might not know what resources are available, and so measuring niche across 20 resources may be the best thing to do. Here though it seems imperative to test using the most relevant data.

It is true that much of the profiling data is not directly related to the experimental conditions (different carbon sources and antibiotics), but in addition to these we do use measurements from experiments carried out in the same environment as the interactions assays (i.e. growth rate and carrying capacity when growing on glucose), which also showed poor correlation with the effects on focals. Additionally, we believe that these profiles contain relevant information regarding metabolic similarity between species (similar to metabolic models often constructed computationally). To improve clarity, we added the following sentence to the figure legend of Figure 3–Figure supplement 1:

"The growth rate, and maximum OD shown in panel A were measured only in M9 glucose, similar to conditions used in the interaction assays." (Lines 591-592)

Additionally and relatedly, it would be valuable to show the scatterplots leading to the conclusion that trait data were uninformative. Pearson's r only works on an assumption of linearity. But there could be strong relationships between the trait data and effect that are monotonic but not linear, or even that are non-monotonic yet still strong (e.g. U-shaped). For the first case, I recommend switching to Spearman's rho over Pearson's r, because it only assumes monotonicity, not linearity. If there are observable relationships that are not monotonic, a different test should be used.

Per your suggestion, we have changed the measurement of correlation in this analysis from Pearson's r, to Spearman's rho. As we observed similar, and still mostly weak correlations, we did not investigate these relationships further. See Figure 3–Figure supplement 1.

Additionally, we generated heat maps including scatterplots mapping the data leading to these correlations. We found no notable dependency in these plots, and visually they were quite crowded and difficult to interpret. As this is not the central point of our study, we ultimately decided against adding this information to the plots.

In general, I think the analyses using the trait data were too simplistic to conclude that the trait data are not predictive.

We agree that more sophisticated analyses may help connect between species traits and their effects on focal species. In fact, other members of our research group have recently used machine learning to accomplish similar predictions (https://doi.org/10.1101/2022.08.02.502471). As such we have changed the wording in to reflect that this correlation is difficult to find using simple analyses:

"These results indicate that it may be challenging to connect the effects of single and pairs of species on a focal strain to a specific trait of the involved strains, using simple analysis." (Lines 157-159)

Author Response

Reviewer #1 (Public Review):

Slusarczyk et al present a very well written manuscript focused on understanding the mechanisms underlying aging of erythrophagocytic macrophages in the spleen (RPM) and its relationship to iron loading with age. The manuscript is diffuse with a broad swath of data elements. Importantly, the manuscript demonstrates that RPM erythrophagocytic capacity is diminished with age, restored in iron restricted diet fed aged mice. In addition, the mechanism for declining RPM erythrophagocytic capacity appears to be ferroptosis-mediated, insensitive to heme as it is to iron, and occur independently of ROS generation. These are compelling findings. However, some of the data relies on conjecture for conclusion and a clear causal association is not clear. The main conclusion of the manuscript points to the accumulation of unavailable insoluble forms of iron as both causing and resulting from decreased RPM erythrophagocytic capacity.

We are proposing that intracellular iron accumulation progresses first and leads to global proteotoxic damage and increased lipid peroxidation. This eventually triggers the death of a fraction of aging RPMs, thus promoting the formation of extracellular iron-rich protein aggregates. More explanation can be found below. Besides, iron loading suppresses the erythrophagocytic activity of RPMs, hence further contributing to their functional impairment during aging.

In addition, the finding that IR diet leads to increased TF saturation in aged mice is surprising.

We believe that this observation implies better mobilization of splenic iron stores, and corroborates our conclusion that mice that age on an iron-reduced diet benefit from higher iron bioavailability, although these differences are relatively mild. More explanation can be found in our replies to Reviewer #2.

Furthermore, whether the finding in RPMs is intrinsic or related to RBC-related changes with aging is not addressed.

We now addressed this issue and we characterized in more detail both iron and ROS levels in RBCs.

Finally, these findings in a single strain and only female mice is intriguing but warrants tempered conclusions.

We tempered the conclusions and provided a basic characterization of the RPM aging phenotype in Balb/c female mice.

Major points:

1) The main concern is that there is no clear explanation of why iron increases during aging although the authors appear to be saying that iron accumulation is both the cause of and a consequence of decreased RPM erythrophagocytic capacity. This requires more clarification of the main hypothesis on Page 4, line 17-18.

We thank the reviewer for this comment. It was previously reported that iron accumulates substantially in the spleen during aging, especially in female mice (Altamura et al., 2014). Since RPMs are those cells that process most of the iron in the spleen, we aimed to explore what is the relationship between iron accumulation and RPM functions during aging. This investigation led us to uncover that indeed iron accumulation is both the cause and the consequence of RPM dysfunction. Specifically, we propose that intracellular iron loading of RPMs precedes extracellular deposition of iron in a form of protein-rich aggregates, driven by RPMs damage. To support this, we now show that the proteome of RPMs overlaps with those proteins that are present in the age-triggered aggregates (Fig. 3F). Furthermore, corroborating our model, we now demonstrate that transient iron loading of RPMs via iron-dextran injection (new Fig. 3G) leads to the formation of protein-rich aggregates, closely resembling those present in aged spleens (new Fig. 3H). This implies that high iron content in RPMs is indeed a major driving factor that leads to aggregation of their proteome and cell damage. Importantly, we now supported this model with studies using iRPMs. We demonstrated that iron loading and blockage of ferroportin by synthetic mini-hepcidin (PR73)(Stefanova et al., 2018) cause protein aggregation in iRPMs and lead to their decreased viability only in cells that were exposed to heat shock, a well-established trigger of proteotoxicity (new Fig. 5K and L). We propose that these two factors, namely age-triggered decrease in protein homeostasis and exposure to excessive iron levels, act in concert and render RPMs particularly sensitive to damage during aging (see also Discussion, p. 16).

In parallel, our data imply that the increased iron content in aged RPMs drives their decreased erythrophagocytic activity, as we now better documented by more extensive in vitro experiments in iRPMs (new Fig 6E-H). We cannot exclude that some of the senescent splenic RBCs that are retained in the red pulp and evade erythrophagocytosis due to RPM defects in aging, may also contribute to the formation of the aggregates. This is supported by the fact that mice that lack RPMs as well exhibit iron loading in the spleen (Kohyama et al., 2009; Okreglicka et al., 2021), and that the proteome of aggregates overlaps to some extent with the proteome of erythrocytes (new Fig. 3F).

We believe that during aging intracellular iron accumulation is chiefly driven by ferroportin downregulation, as also suggested by Reviewer#3. We now show that ferroportin drops significantly already in mice aged 4 and 5 months (new Fig. 4H), preceding most of the other impairments. This drop coincides with the increase in hepcidin expression, but if this is the sole reason for ferroportin suppression during early aging would require further investigation outside the scope of the present manuscript.

In sum, to address this comment, we now modified the fragment of the introduction that refers to our hypothesis and major findings to be more clear (p. 4), we improved our manuscript by providing new data mentioned above and we added more explanation in the corresponding sections of the Results and Discussion.

2) It is unclear if RPMs are in limited supply. Based on the introduction (page 4, line 13-15), they have limited self-renewal capacity and blood monocytes only partially replenished. Fig 4D suggests that there is a decrease in RPMs from aged mice. The %RPM from CD45+ compartment suggests that there may just be relatively more neutrophils or fewer monocytes recruited. There is not enough clarity on the meaning of this data point.

Thank you for this comment. We fully agree that %RPMs of CD45+ splenocytes, although well-accepted in literature (Kohyama et al., 2009; Okreglicka et al., 2021), is only a relative number. Hence, we now included additional data and explanations regarding the loss of RPMs during aging.

It was reported that the proportion of RPMs derived from bone marrow monocytes increases mildly but progressively during aging (Liu et al., 2019). This implies that due to the loss of the total RPM population, as illustrated by our data, the cells of embryonic origin are likely even more affected. We could confirm this assumption by re-analysis of the data from Liu et al. that we now included in the manuscript as Fig. 5E. These data clearly show that the representation of embryonically-derived RPMs drops more drastically than the percent of total RPMs, whereas the replenishment rate from monocytes is not affected significantly during aging. Consistent with this, we have not observed any robust change in the population of monocytes (F4/80-low, CD11b-high) or pre-RPMs (F4/80-high, CD11b-high) in the spleen at the age of 10 months (Figure 5-figure supplement 2A and B). We also have detected a mild decrease, not an increase, in the number of granulocytes (new Figure 5-figure supplement 2C). Furthermore, we measured in situ apoptosis marker and found a clear sign of apoptosis in the aged spleen (especially in the red pulp area), a phenotype that is less pronounced in mice on an IR diet (new Fig. 5O). This is consistent with the observation that apoptosis markers can be elevated in tissues upon ferroptosis induction (Friedmann Angeli et al., 2014) and that the proteotoxic stress in aged RPMs, which we now emphasized better in our manuscript, may also lead to apoptosis (Brancolini & Iuliano, 2020). Taken together, we strongly believe that the functional defect of embryonically-derived RPMs chiefly contributes to their shortage during aging.

3) Anemia of aging is a complex and poorly understood mechanistically. In general, it is considered similar to anemia of chronic inflammation with increased Epo, mild drop in Hb, and erythroid expansion, similar to ineffective erythropoiesis / low Epo responsiveness. It is not surprising that IR diet did not impact this mild anemia. However, was the MCV or MCH altered in aged and IR aged mice?

We now included the data for hematocrit, RBC counts, MCV, and MCH in Figure 1-figure supplement 5. Hematocrit shows a similar tendency as hemoglobin levels, but the values for RBC counts, MCV, and MCH seem not to be altered. We also show now that the erythropoietic activity in the bone marrow is not affected in aged versus young mice. Taken together, the anemic phenotype in female C57BL/6J mice at this age is very mild, which we emphasized in the main text, and is likely affected by other factors than serum iron levels (p. 6).

4) Page 6, line 23 onward: the conclusion is that KC compensate for the decreased function of RPM in the spleen, based on the expansion of KC fraction in the liver. Is there evidence that KCs are engaged in more erythrophagocytosis in aged mice? Furthermore, iron accumulation in the liver with age does not demonstrate specifically enhanced erythrophagocytosis of KC. Please clarify why liver iron accumulation would not be simply a consequence of increased parenchymal iron similar to increased splenic iron with age, independent of erythrophagocytic activity in resident macrophages in either organ.

Thanks for these questions. For the quantification of the erythrophagocytosis rate in KC, we show, as for the RPMs (Fig. 1K), the % of PKH67-positive macrophages, following transfusion of PKH67-stained stressed RBCs (Fig. 1M). The data implies a mild (not statistically significant) drop (of approx. 30%) in EP activity. We believe that it is overridden by a more pronounced (on average, 2-fold) increase in the representation of KCs (Fig. 1N). The mechanisms of iron accumulation between the spleen and the liver are very different. In the liver, we observed iron deposition in the parenchymal cells (not non-parenchymal, new Fig. 1P) that we currently characterizing in more detail in a parallel manuscript. Our data demonstrate a drop in transferrin saturation in aged mice. Hence, it is highly unlikely that aging would be hallmarked by the presence of circulating non-transferrin-bound iron that would be sequestered by hepatocytes, as shown previously (Jenkitkasemwong et al., 2015). Thus, the iron released locally by KCs is the most likely contributor to progressive hepatocytic iron loading during aging. The mechanism of iron delivery to hepatocytes from erythrophagocytosing KCs was demonstrated by Theurl et al.(Theurl et al., 2016), and we propose that it may be operational, although in a much more prolonged time scale, during aging. We now discussed this part better in our Results sections (p. 7).

5) Unclear whether the effect on RPMs is intrinsic or extrinsic. Would be helpful to evaluate aged iRPMs using young RBC vs. young iRPMs using old RBCs.

We are skeptical if the generation of iRPMs cells from aged mice would be helpful – these cells are a specific type of primary macrophage culture, derived from bone marrow monocytes with MCSF1, and exposed additionally to heme and IL-33 for 4 days. We do not expect that bone marrow monocytes are heavily affected by aging, and would thus recapitulate some aspects of aged RPMs from the spleen, especially after 8-day in vitro culture. However, to address the concerns of the reviewer, we now provide additional data regarding RBC fitness. Consistent with the time life-span experiment (Fig, 2A), we show that oxidative stress in RBCs is only increased in splenic, but not circulating RBCs (new Fig. 2C, replacing the old Fig. 2B and C). In addition, we show no signs of age-triggered iron loading in RBCs, either in the spleen (new Fig. 2F) or in the circulation (new Fig. 2B). Hence, we do not envision a possibility that RPMs become iron-loaded during aging as a result of erythrophagocytosis of iron-loaded RBCs. In support of this, we also have observed that during aging first RPMs’ FPN levels drop, afterward erythrophagocytosis rate decreases, and lastly, RBCs start to exhibit significantly increased oxidative stress (presented now in new Fig. 4H, J and K).

6) Discussion of aggregates in the spleen of aged mice (Fig 2G-2K and Fig 3) is very descriptive and non-specific. For example, if the iron-rich aggregates are hemosiderin, a hemosiderin-specific stain would be helpful. This data specifically is correlatory and difficult to extract value from.

Thanks for these comments. To the best of our knowledge Prussian blue Perls’ staining (Fig. 2J) is considered a hemosiderin staining. Our investigations aimed to better understand the nature and the origin of splenic iron deposits that to some extent are referred to as hemosiderin. Most importantly, as mentioned in our reply R1 Ad. 1. to assign causality to our data, we now demonstrated that iron accumulation in RPMs in response to iron-dextran (Fig. 3G) increases lipid peroxidation (Fig. 5F), tends to provoke RPMs depletion (Fig. 5G) and triggers the formation of protein-rich aggregates (new Fig. 3H). Of note, we assume that the loss of embryonically-derived RPMs in this model may be masked by simultaneous replenishment of the niche from monocytes, a phenomenon that may be addressed by future studies using Ms4a3-driven reporter mice (as shown for aged mice in our new Fig. 5E).

7) The aging phenotype in RPMs appears to be initiated sometime after 2 months of age. However, there is some reversal of the phenotype with increasing age, e.g. Fig 4B with decreased lipid peroxidation in 9 month old relative to 6 month old RPMs. What does this mean? Why is there a partial spontaneous normalization?

Thanks for this comment and questions. Indeed, the degree of lipid peroxidation exhibits some kinetics, suggestive of partial normalization. Of note, such a tendency is not evident for other aging phenotypes of RPMs, hence, we did not emphasize this in the original manuscript. However, in a revised version of the manuscript, we now present the re-analysis of the published data which implies that the number of embryonically-derived RPMs drops substantially between mice at 20 weeks and 36 weeks (new Fig. 5E). We think that the higher proportion of monocyte-derived RPMs in total RPM population later in aging (9 months) might be responsible for the partial alleviation of lipid peroxidation. We now discussed this possibility in the Results sections (p. 12).

8) Does the aging phenotype in RPMs respond to ferristatin? It appears that NAC, which is a glutathione generator and can reverse ferroptosis, does not reverse the decreased RPM erythrophagocytic capacity observed with age yet the authors still propose that ferroptosis is involved. A response to ferristatin is a standard and acceptable approach to evaluating ferroptosis.

We fully agree with the Reviewer that using ferristatin or Liproxstatin-1 would be very helpful to fully characterize a mechanism of RPMs depletion in mice. However, previous in vivo studies involving Liproxstatin-1 administration required daily injections of this ferroptosis inhibitor (Friedmann Angeli et al., 2014). This would be hardly feasible during aging. Regarding the experiments involving iron-dextran injection, using Liproxstatin-1 would require additional permission from the ethical committee which takes time to be processed and received. However, to address this question we now provide data from iRPMs cell cultures (new Fig.5 K-L). In essence, our results imply that both proteotoxic stress and iron overload act in concert to trigger cytotoxicity in RPM in vitro model. Interestingly, this phenomenon does not depend solely on the increased lipid peroxidation, but when we neutralize the latter with Liproxstatin-1, the cytotoxic effect is diminished (please, see also Results on p. 13 and Discussion p. 15/16).

9) The possible central role for HO-1 in the pathophysiology of decreased RPM erythrophagocytic capacity with age is interesting. However, it is not clear how the authors arrived at this hypothesis and would be useful to evaluate in the least whether RBCs in young vs. aged mice have more hemoglobin as these changes may be primary drivers of how much HO-1 is needed during erythrophagocytosis.

Thanks for this comment. We got interested in HO-1 levels based on the RNA sequencing data, which detected lower Hmox-1 expression in aged RPMs (Figure 3-figure supplement 1). We now show that the content of hemoglobin is not significantly altered in aged RBCs (MCH parameter, Figure 1-figure supplement 5E), hence we do not think that this is the major driver for Hmox-1 downregulation. Likewise, the levels of the Bach1 message, a gene encoding Hmox-1 transcriptional repressor, are not significantly altered according to RNAseq data. Hence, the reason for the transcriptional downregulation of Hmox-1 is not clear. Of note, HO-1 protein levels in the total spleen are higher in aged versus young mice, and we also detected a clear appearance of its nuclear truncated and enzymatically-inactive form (see a figure below, we opt not to include this in the manuscript for better clarity). The appearance of truncated HO-1 seems to be partially rescued by the IR diet. It is well established that the nuclear form of HO-1 emerges via proteolytic cleavage and migrates to the nucleus under conditions of oxidative stress (Mascaro et al., 2021). This additionally confirms that the aging spleen is hallmarked by an increased burden of ROS. Moreover, we also detected HO-1 as one of the components of the protein iron-rich aggregates. Thus, we propose that the low levels of the cytoplasmic enzymatically active form of HO-1 in RPMs (that we preferentially detect with our intracellular staining and flow cytometry) may be underlain by its nuclear translocation and sequestration in protein aggregates that evade antibody binding [this is also supported by our observation that the protein aggregates, despite the high content of ferritin (as indicated by MS analysis) are negative for L-ferritin staining. Of note, we also cannot exclude that other cell types in the aging spleen (eg. lymphocytes) express higher levels of HO-1 in response to splenic oxidative stress.

Fig. Total splenic levels of HO-1 in young, aged IR and aged mice.

Reviewer #2 (Public Review):

Slusarczyk et al. investigate the functional impairment of red pulp macrophages (RPMs) during aging. When red blood cells (RBCs) become senescent, they are recycled by RPMs via erythrophagocytosis (EP). This leads to an increase in intracellular heme and iron both of which are cytotoxic. The authors hypothesize that the continuous processing of iron by RPMs could alter their functions in an age-dependent manner. The authors used a wide variety of models: in vivo model using female mice with standard (200ppm) and restricted (25ppm) iron diet, ex vivo model using EP with splenocytes, and in vitro model with EP using iRPMs. The authors found iron accumulation in organs but markers for serum iron deficiency. They show that during aging, RPMs have a higher labile iron pool (LIP), decreased lysosomal activity with a concomitant reduction in EP. Furthermore, aging RPMs undergo ferroptosis resulting in a non-bioavailable iron deposition as intra and extracellular aggregates. Aged mice fed with an iron restricted diet restore most of the iron-recycling capacity of RPMs even though the mild-anemia remains unchanged.

Overall, I find the manuscript to be of significant potential interest. But there are important discrepancies that need to be first resolved. The proposed model is that during aging both EP and HO-1 expression decreases in RPMs but iron and ferroportin levels are elevated. In their model, the authors show intracellular iron-rich proteinaceous aggregates. But if HO-1 levels decrease, intracellular heme levels should increase. If Fpn levels increase, intracellular iron levels should decrease. How does LIP stay high in RPMs under these conditions? I find these to be major conflicting questions in the model.

We thank the Reviewer for her/his valuable feedback. As we mentioned in our replies we can only assume that a small misunderstanding in the interpretation of the presented data underlies this comment. We show that ferroportin levels in RPMs (Fig. 1F) are modulated in a manner that fully reflects the iron status of these cells (both labile and total iron levels, Figs. 1H and I). FPN levels drop in aged RPMs and are rescued when mice are maintained on a reduced iron diet. As pointed out by Reviewer#3, and explained in our replies we believe that ferroportin levels are critical for the observed phenotypes in aging. We now described our data in a more clear way to avoid any potential misinterpretation (p.6).

Reviewer #3 (Public Review):

This is a comprehensive study of the effects of aging of the function of red pulp macrophages (RPM) involved in iron recycling from erythrocytes. The authors document that insoluble iron accumulates in the spleen, that RPM become functionally impaired, and that these effects can be ameliorated by an iron-restricted diet. The study is well written, carefully done, extensively documented, and its conclusions are well supported. It is a useful and important addition for at least three distinct fields: aging, iron and macrophage biology.

The authors do not explain why an iron-restricted diet has such a strong beneficial effect on RPM aging. This is not at all obvious. I assume that the number of erythrocytes that are recycled in the spleen, and are by far the largest source of splenic iron, is not changed much by iron restriction. Is the iron retention time in macrophages changed by the diet, i.e. the recycled iron is retained for a short time when diet is iron-restricted (making hepcidin low and ferroportin high), and long time when iron is sufficient (making hepcidin high and ferroportin low)? Longer iron retention could increase damage and account for the effect. Possibly, macrophages may not empty completely of iron before having to ingest another senescent erythrocyte, and so gradually accumulate iron.

We are very grateful to this Reviewer for emphasizing the importance of the iron export capacity of RPMs as a possible driver of the observed phenotypes. Indeed, as mentioned above, we now show in the revised version of the manuscript that ferroportin drops early during aging (revised Fig. 4). Importantly, we now also observed that iron loading and limitation of iron export from iRPMs via ferroportin aggravate the impact of heat shock (a well-accepted trigger of proteotoxicity) on both protein aggregation and cell viability (new Fig. 5K and L). Physiologically, recent findings show that aging promotes a global decrease in protein solubility [BioRxiv manuscript (Sui X. et al., 2022)], and it is very likely that the constant exposure of RPMs to high iron fluxes renders these specialized cells particularly sensitive to proteome instability. This could be further aggravated by a build-up of iron due to the drop of ferroportin early during aging, ultimately leading to the appearance of the protein aggregates as early as at 5 months of age in C57BL/6J females. Based on the new data, we emphasized this model in the revised version of the manuscript (please, see Discussion on p. 16)

Author Response

Reviewer #1 (Public Review):

1) It would be helpful to include some sort of comparison in Fig. 4, e.g. the regressions shown in Fig 3, to indicate to what extent the ICCl data corresponds to the "control range" of frequency tuning.

Figure 4 was modified to show the frequency range typically found in the ICCls. This range is based on results from Wagner et al., 2007, which extensively surveyed ICCls responses. This modification shows that our ICCls recordings in the ruff-removed owls cover the normal frequency hearing range of the owl.

2) A central hypothesis of the study is that the frequency preference of the high-frequency neurons is lower in ruff-removed owls because of the lowered reliability caused by a lack of the ruff. Yet, while lower, the frequency range of many neurons in juvenile and ruff-removed owls seems sufficiently high to be still responsive at 7-8 kHz. I think it would be important to know to what extent neurons are still ITD sensitive at the "unreliable high frequencies" even if the CFs are lower since the "optimization" according to reliability depends not on the best frequency of each neuron per se, but whether neurons are less ITD sensitive at the higher, less reliable frequencies.

The concern regarding the frequency range that elicits responsivity was largely addressed above. Specifically, Figure L1 showing frequency tuning of frontally tuned ICx neurons in ruff-removed owls indicates that while there is some variability of tuning across neurons, there is little responsivity above 6 kHz. In contrast, equivalent analysis in juvenile owls (Figure L3), shows there is much more responsiveness and variability across neurons to high and low frequencies. This evidence supports our hypothesis that the juvenile owl brain is still highly plastic, which facilitates learning during development. Although the underlying data was already reported in Figure 7 of our previously submitted manuscript, we can include Figures L1 and L2, potentially as supplemental figures, if considered useful by editors and reviewers. Nevertheless, this argumentation was further expanded in the revised text (Line 229).

Figure L1. Frequency tuning of frontally-tuned ICx neurons in ruff-removed owls. Tuning curves are normalized by the max response. Thick black line indicates the average tuning curve. Dashed black line indicates basal response.

Figure L2. ITD sensitivity across frequencies in ruff-removed owl. Two example neurons shown in a and b. ITD tuning for tones (colored) and broadband (black) plotted by firing rate (non-normalized). Solid colored lines indicate responses to frequencies that are within the neuron’s preferred frequency range (i.e. above the half-height, see Methods), dashed lines indicate frequencies outside of the neuron’s frequency range.

Figure L3. Frequency tuning of frontally-tuned ICx neurons in juvenile owls. Tuning curves are normalized by the max response. Thick black line indicates the average tuning curve. Dashed black line indicates basal response.

3) It would be interesting to have an estimate of the time scale of experience dependency that induces tuning changes. Do the authors have any data on this question? I appreciate the authors' notion that the quantifications in Fig 7 might indicate that juvenile owls are already "beginning to be shaped by ITD reliability" (line 323 in Discussion). How many days after hearing onset would this correspond to? Does this mean that a few days will already induce changes?

While tracking changes induced by ruff-removal over development were outside of the scope of this study, many other studies have assessed experience-dependent plasticity in the barn owl. The recordings in this study were performed approximately 20 days after hearing onset, suggesting that the juveniles had ample time to begin learning. These points were expanded upon in the discussion (Lines 254, 280-283).

Reviewer #2 (Public Review):

1) Why is IPD variability plotted instead of ITD variability (or indeed spatial reliability)? The relationship between these measures is likely to vary across frequency, which makes it difficult to compare ITD variability across frequency when IPDs are plotted. Normalizing data across frequencies also makes it difficult to compare different locations and acoustical conditions. For example, in Fig.1a and Fig.1b, the data shown for 3 kHz at ~160 degrees seems quantitatively and visually quite different, but the difference (in Fig.1c) appears to be negligible.

Justification of why IPD variability is used as an estimate of ITD variability was added to introduction (Lines 55-60), results (Line 100) and methods (Lines 371-374) sections of the manuscript, explaining the fact that because ITD detection is based on phase locking by auditory nerve and ITD detector neurons tuned to narrow frequency bands, responses of ITD detector neurons forwarded to downstream midbrain regions are therefore determined by IPD variability. Additionally, ITD is calculated by dividing IPD by frequency, which makes comparisons of ITD reliability across frequency mathematically uninformative.

2) How well do the measures of ITD reliability used reflect real-world listening? For example, the model used to calculate ITD reliability appears to assume the same (flat) spectral profile for targets and distractors, which are presented simultaneously with the same temporal envelope, and a uniform spatial distribution of sounds across space. It is therefore unclear how robust the study's results are to violations of these assumptions.

While we agree that our analysis cannot completely capture real-world listening for the barn owl, a general analysis using similar flat spectral profiles for targets and concurrent sounds provides a broad assessment of reliability of ITD cues. While a full recapitulation of real-world listening is beyond the scope of this study (i.e. recording natural scenes from the ear canals of wild barn owls), we included additional analyses of ITD reliability in Figure 1-figure supplement 1, described above.

3) Does facial ruff removal produce an isolated effect on ITD variability or does it also produce changes in directional gain, and the relationship between spatial cues and sound location? Although the study considers this issue in some places (e.g. Fig.2, Fig.5), a clearer presentation of the acoustical effects of facial ruff removal and their implications (for all locations, not just those to the front), as well as an attempt to understand how these acoustical changes lead to the observed changes in ITD reliability, would greatly strengthen the study. In addition, Fig.1 shows average ITD reliability across owls, but it would be helpful to know how consistent these measures are across owls, given individual variability in Head-Related Transfer Functions (HRTFs). This potentially has implications for the electrophysiological experiments, if the HRTFs of those animals were not measured. One specific question that is potentially very relevant is whether the facial ruff attenuates sounds presented behind the animal and whether it does so in a frequency-dependent way. In addition, if facial ruff removal enables ILDs to be used for azimuth, then ITDs may also become less necessary at higher frequencies, even if their reliability remains unchanged.

Additional analysis was conducted to generate representation of changes in directional gain induced by ruff removal, added to new figure (Fig 5). This analysis shows that changes in gain following ruff-removal are largely frequency-independent: there is a de-attenuation of peripherally and rearwardly located sounds, but the highest gain remains for high frequencies in frontal space. There is an additional increase in gain for high frequencies from rearward space, these changes would not explain the changes in frequency tuning we report. As mentioned in new additions to the manuscript, the changes at the most rearward-located auditory spatial locations are unlikely to have an effect on the auditory midbrain. No studies in the barn owl have found neurons in the ICx or optic tectum tuned to >120° (Knudsen, 1982; Knudsen, 1984; Cazettes et al., 2014). In addition, variability of IPD reliability across owls was analyzed and reported in the amended Figure 1, which notes very little changes across owls. In this analysis, we did realize that the file of one of the HRTFs obtained from von Campenhausen et al. 2006 was mislabeled, which explains slight differences in revised Fig 1b. Nevertheless, added analysis of IPD reliability across owls indicates that the pattern in ITD reliability is stable across owls (Fig. 1d,e), which supports our decision to not record HRTFs from owls used in this study. Finally, we added to the discussion that clarifies that the use of ILD for azimuth would not provide the same resolution as ITD would (Lines 295-303). We also do not believe that the use of ILD for azimuth would make “ITDs… less necessary at higher frequencies”, given that the ICCls is still computing ITD at these high frequencies (Fig 4), and that ILDs also have higher resolution at higher frequencies, with and without the facial ruff (Olsen et al, 1989; Keller et al., 1998; von Campenhausen et al., 2006).

1) It is unclear why some analyses (Fig.5, Fig.7) are focused on frontal locations and frontally-tuned neurons. It is also unclear why neurons with a best ITDs of 0 are described as frontally tuned since locations behind the animal produce an ITD of 0 also. Related to this, in Fig.1, facial ruff removal appears to reduce IPD variability at low frequencies for locations to the rear (~160 degrees), where the ITD is likely to be close to 0. Neurons with a best ITD of 0 might therefore be expected to adjust their frequency tuning in opposite directions depending on whether they are tuned to frontal or rearward locations.

An extensive explanation was added to the methods detailing why we do not believe the neurons recorded in this study are tuned to the rear. Namely, studies mapping the barn owl’s ICx and optic tectum have not reported neurons tuned to locations >120°, with the number of neurons representing a given spatial location decreasing with eccentricity (Knudsen, 1982; Knudsen, 1984; Cazettes et al., 2014). While we agree that there does seem to be a change in ITD reliability at ~160° following ruff-removal, the result is largely similar to the change that occurs in frontal space (Fig 1b), which is consistent with the ruff-removed head functioning as a sphere. Thus, we wouldn’t expect rearwardly-tuned neurons, if they could be readily found, to adjust their frequency tuning to higher frequencies. Finally, we want to clarify that we focused our analyses on frontally-tuned neurons because frontal space is where we observed the largest change in ITD reliability. Text was added to the Discussion section to clarify this point (Lines 313-321).

2) The study suggests that information about high-frequency ITDs is not passed on to the ICX if the ICX does not contain neurons that have a high best frequency. However, neurons might be sensitive to ITDs at frequencies other than the best frequency, particularly if their frequency tuning is broader. It is also unclear whether the best frequency of a neuron always corresponds to the frequency that provides the most reliable ITD information, which the study implicitly assumes.

The concern about ITD sensitivity at non-preferred frequencies was addressed under the essential revision #3, as well as under Reviewer 1’s concerns.

Author Response

Reviewer #1 (Public Review):

This manuscript reports a systematic study of the cortical propagation patterns of human beta bursts (~13-35Hz) generated around simple finger movements (index and middle finger button presses).

The authors deployed a sophisticated and original methodology to measure the anatomical and dynamical characteristics of the cortical propagation of these transient events. MEG data from another study (visual discrimination task) was repurposed for the present investigation. The data sample is small (8 participants). However, beta bursts were extracted over a +/- 2s time window about each button press, from single trials, yielding the detection and analysis of hundreds of such events of interest. The main finding consists of the demonstration that the cortical activity at the source of movement related beta bursts follows two main propagation patterns: one along an anteroposterior directions (predominantly originating from pre central motor regions), and the other along a medio- lateral (i.e., dorso lateral) direction (predominantly originating from post central sensory regions). Some differences are reported, post-hoc, in terms of amplitude/cortical spread/propagation velocity between pre and post-movement beta bursts. Several control tests are conducted to ascertain the veracity of those findings, accounting for expected variations of signal-to-noise ration across participants and sessions, cortical mesh characteristics and signal leakage expected from MEG source imaging.

One major perceived weakness is the purely descriptive nature of the reported findings: no meaningful difference was found between bursts traveling along the two different principal modes of propagation, and importantly, no relation with behavior (response time) was found. The same stands for pre vs. post motor bursts, except for the expected finding that post-motor bursts are more frequent and tend to be of greater amplitude (yielding the observation of a so-called beta rebound, on average across trials).

Overall, and despite substantial methodological explorations and the description of two modes of propagation, the study falls short of advancing our understanding of the functional role of movement related beta bursts.

For these reasons, the expected impact of the study on the field may be limited. The data is also relatively limited (simple button presses), in terms of behavioral features that could be related to the neurophysiological observations. One missed opportunity to explain the functional role of the distinct propagation patterns reports would have been, for instance, to measure the cortical "destination" of their respective trajectories.

In response to this comment, we would like to highlight two important points.

First, our work constitutes the first non-invasive human confirmation of invasive work in animals (Balasubramanian et al., 2020; Roberts et al., 2019; Rule et al., 2018; (Balasubramanian et al., 2020; Best et al., 2016; Rubino et al., 2006; Takahashi et al., 2011, 2015) and patients (Takahashi et al., 2011). Thus, these results bridges between recordings limited to the size of multielectrode arrays (roughly 0.16 cm2; Balasubramanian et al., 2020; Best et al., 2016; Rubino et al., 2006; Takahashi et al., 2011, 2015) and human EEG recordings spanning across large areas of the cortex and several functionally distinct regions (Alexander et al., 2016; Stolk et al., 2019). The ability to access these neural signatures non- invasively is important for cross-species comparison. This further enables us, to provide an in-depth analysis of the spatiotemporal diversity of human MEG signals and a detailed characterisation of the two propagation directions, which significantly extends previous reports. We note that their functional role remains undetermined also in these animal studies, but being able to identify these signals now in humans can provide a steppingstone for identifying their role.

Second, and related, the reviewers are correct that we did not observe distinct propagation directions between pre- and post-movement bursts, nor a relationship with reaction time. However, such a null result would be relevant, in our view, towards understanding what the functional relevance of these signals, if any, might be. Recent work in macaques indicates that the spatiotemporal patterns of high-gamma activity carry kinematic information about the upcoming movement (Liang et al 2023). The functional role of beta may therefore be more complex and not relate to reaction times or kinematics in a straightforward manner. We believe this is a relevant observation, and in keeping with the continued efforts to identify how sensorimotor beta relates to behaviour. It is increasingly clear that spatiotemporal diversity in animal recordings and human E/MEG and intracranial recordings can constitute a substantial proportion of the measured dynamics. As such, our report is relevant in narrowing down what these signals may reflect.

Together, we think that our work provides new insights into the multidimensional and propagating features of burst activity. This is important for the entire electrophysiology community, as it transforms how we commonly analyse and interpret these important brain signals. We anticipate that our work will guide and inspire future work on the mechanistic underpinnings of these dominant neural signals. We are confident that our article has the scope to reach out to the diverse readership of eLife.

Reviewer #2 (Public Review):

The authors devised novel and interesting experiments using high precision human MEG to demonstrate the propagation of beta oscillation events along two axes in the brain. Using careful analysis, they show different properties of beta events pre- and post movement, including changes in amplitude. Due to beta's prominent role in motor system dynamics, these changes are therefore linked to behavior and offer insights into the mechanisms leading to movement. The linking of wave-like phenomena and transient dynamics in the brain offers new insight into two paradigms about neural dynamics, offering new ways to think about each phenomena on its own.

Although there is a substantial, and recent, body of literature supporting the conclusions that beta and other neural oscillations are transient, care must be taken when analyzing the data and the resulting conclusions about beta properties in both time and space. For example, modifying the threshold at which beta events are detected could alter their reported properties and expression in space and time. The authors should therefore performing parameter sweeps on e.g. the thresholds for detection of oscillation bursts to determine whether their conclusions on beta properties and propagation hold. If this additional analysis does not change their story, it would lend confidence in the results/conclusions.

We thank the reviewing team for this comment. As suggested, we evaluated the effect of different burst thresholds on the burst parameters.

The threshold in the main analysis was determined empirically from the data, as in previous work (Little et al., 2019). Specifically, trial-wise power was correlated with the burst probability across a range of different threshold values (from median to median plus seven standard deviations (std), in steps of 0.25, see Figure 6-figure supplement 1). The threshold value that retained the highest correlation between trial-wise power and burst probability was used to binarize the data.

We repeated our original analysis using four additional thresholds, i.e., original threshold - 0.5 std, -0.25 std, +0.25 std, +0.5 std. As one would expect, burst threshold is negatively related to the number of bursts (i.e., higher thresholds yield fewer bursts, Figure R4a [top]), and positively related to burst amplitude (i.e., higher thresholds yield higher burst amplitudes, Figure R4a [bottom]).

Similarly, the temporal duration of bursts and apparent spatial width are modulated by the burst threshold: lowering the threshold leads to longer temporal duration and larger apparent spatial width while increasing the threshold leads to shorter temporal duration and smaller apparent spatial width Figure R4b. Note that for the temporal and spectral burst characteristics, the difference to the original threshold can be numerically zero, i.e., changing the burst threshold did not lead to changes exceeding the temporal and spectral resolution of the applied time-frequency transformation (i.e., 200ms and 1Hz respectively).

Importantly, across these threshold values, the propagation direction and propagation speed remain comparable.

We now include this result as Figure 6-figure supplement 2and refer to this analysis in the manuscript (page 28 line 717).

“To explore the robustness of the results analyses were repeated using a range of thresholds (Figure 6-figure supplement 2).”

Determining the generators of beta events at different locations is a tricky issue. The authors mentioned a single generator that is responsible for propagating beta along the two axes described. However, it is not clear through what mechanism the beta events could travel along the neural substrate without additional local generators along the way. Previous work on beta events examined how a sequence of synaptic inputs to supra and infragranular layers would contribute to a typical beta event waveform. Although it is possible other mechanisms exist, how might this work as the beta events propagate through space? Some further explanation/investigation on these issues is therefore warranted.

Based on this and other comments (i.e., comments 7 and 8) we re-evaluated the use of the term ‘generator’ in this manuscript.

While the term generator can be used across scales, from micro- to macroscale, ifor the purpose of the present paper, we believe one should differentiate at least two concepts: a) generator of beta bursts, and b) generator of travelling waves.

We realised that in the previous version of the manuscript the term ‘generator’ was at times used without context. We removed the term where no longer necessary.

Further, the previous version of the manuscript discussed putative generators of travelling waves (page 19f.) but not generators of beta bursts. We now address this as follows:

“Studies using biophysical modelling have proposed that beta bursts are generated by a broad infragranular excitatory synaptic drive temporally aligned with a strong supragranular synaptic drive (Law et al., 2022; Neymotin et al., 2020; Sherman et al., 2016; Shin et al., 2017) whereby layer specific inhibition acts to stabilise beta bursts in the temporal domain (West et al., 2023). The supragranular drive is thought to originate in the thalamus (E. G. Jones, 1998, 2001; Mo & Sherman, 2019; Seedat et al., 2020), indicating thalamocortical mechanisms (page 22f).”

Once the mechanisms have been better understood, a question of how much the results generalize to other oscillation frequencies and other brain areas. On the first question of other oscillation frequencies, the authors could easily test whether nearby frequency bands (alpha and low gamma) have similar properties. This would help to determine whether the observations/conclusions are unique to beta, or more generally applicable to transient bursts/waves in the brain. On the second issue of applicability to other brain areas, the authors could relate their work to transient bursts and waves recorded using ECoG and/or iEEG. Some recent work on traveling waves at the brain-wide level would be relevant for such comparisons.

We appreciate the enthusiasm and the suggestions. To comment on the frequency specificity of the observed effects we conducted the same analysis focusing on the gamma frequency range (60-90 Hz). For computational reasons, we limited this analysis to one subject. Figure R1 shows the polar probability histogram for the beta frequency range (left) and the gamma frequency range (right). In contrast to the beta frequency range, no dominant directions were observed for the gamma range and von Mises functions did not converge. These preliminary results suggest some frequency specificity of the spatiotemporal pattern in sensorimotor beta activity. We believe this paves the way for future analysis mapping propagation direction across frequency and space.

Here we did not investigate the spatial specificity of the effects, as the beta frequency range is dominant in sensorimotor areas. Investigating beta bursts in other cortical areas would have likely resulted in very few bursts. We discuss our results across spatial scales in the section: Distinct anatomical propagation axes of sensorimotor beta activity. However, please note that most of the previous literature operates on a different spatial scale (roughly 4mm; Balasubramanian et al., 2020; Best et al., 2016; Rubino et al., 2006; Rule et al., 2018; Takahashi et al., 2011, 2015) and different species (e.g., non-human primates). Non-invasive recordings in humans capture temporospatial patterns of a very different scale, i.e., often across the whole cortex (Alexander et al., 2016; Roberts et al., 2019). Comparing spatiotemporal patterns, across different spatial scales is inherently difficult. Work

investigating different spatial scales simultaneously, such as Sreekumar et al. 2020, is required to fully unpack the relationship between mesoscopic and macroscopic spatiotemporal patterns.

Figure R1: Spatiotemporal organisation for the beta (β, 13-30Hz) and gamma (γ, 60-90) frequency range for one exemplar subject. Same as Figure 4a, but for one exemplar subject.

If the source code could be provided on github along with documentation and a standard "notebook" on use other researchers would benefit greatly.

All analyses are performed using freely available tools in MATLAB. The code carrying out the analysis in this paper can be found here: [link provided upon acceptance]. The 3D burst analyses can be very computationally intensive even on a modern computer system. The analyses in this paper were computed on a MacBook Pro with a 2.6 GHz 6-Core Intel Core i7 and 32 Gb of RAM. Details on the installation and setup of the dependencies can be found in the README.md file in the main study repository.

This information has been added to the paper in the methods section on page 35.

Author Response

Reviewer #1 (Public Review):

This manuscript provides a comprehensive investigation of the effects of the genetic ablation of three different transcription factors (Srf, Mrtfa, and Mrtfb) in the inner ear hair cells. Based on the published data, the authors hypothesized that these transcription factors may be involved in the regulation of the genes essential for building the actin-rich structures at the apex of hair cells, the mechanosensory stereocilia and their mechanical support - the cuticular plate. Indeed, the authors found that two of these transcription factors (Srf and Mrtfb) are essential for the proper formation and/or maintenance of these structures in the auditory hair cells. Surprisingly, Srf- and Mrtfb- deficient hair cells exhibited somewhat similar abnormalities in the stereocilia and in the cuticular plates even though these transcription factors have very different effects on the hair cell transcriptome. Another interesting finding of this study is that the hair cell abnormalities in Srfdeficient mice could be rescued by AAV-mediated delivery of Cnn2, one of the downstream targets of Srf. However, despite a rather comprehensive assessment of the novel mouse models, the authors do not have yet any experimentally testable mechanistic model of how exactly Srf and Mrtfb contribute to the formation of actin cytoskeleton in the hair cells. The lack of any specific working model linking Srf and/or Mrtfb with stereocilia formation decreases the potential impact of this study.

Major comments:

Figures 1 & 3: The conclusion on abnormalities in the actin meshwork of the cuticular plate was based largely on the comparison of the intensities of phalloidin staining in separate samples from different groups. In general, any comparison of the intensity of fluorescence between different samples is unreliable, no matter how carefully one could try matching sample preparation and imaging conditions. In this case, two other techniques would be more convincing: 1) quantification of the volume of the cuticular plates from fluorescent images; and 2) direct examination of the cuticular plates by transmission electron microscopy (TEM).

In fact, the manuscript provides no single TEM image of the F-actin abnormalities either in the cuticular plate or in the stereocilia, even though these abnormalities seem to be the major focus of the study. Overall, it is still unclear what exactly Srf or Mrtfb deficiencies do with F-actin in the hair cells.

Yes, we agree. As suggested by the reviewer, to directly examine the defects in F-actin organization within the cuticular plate of mutant mice, we conducted Transmission Electron Microscopy (TEM) analyses. The results, as presented in the revised Figures 1 and 4 (panels F, G, and E, F, respectively), provide crucial insights into the structural changes in the cuticular plate. Meanwhile, the comparison of the volume of the phalloidin labeled cuticular plate after 3-D reconstruction using Imaris software was conducted and shown in Author response image 1. The results of the cuticular plate (CP) volume were consistent with the relative F-actin intensity change of the cuticular plate in the revised Figures 1B and 4B. For the TEM analysis of the stereocilia, we regret that due to time constraints, we were unable to collect TEM images of stereocilia with sufficient quality for a meaningful comparison. However, we believe that the data we have presented sufficiently addresses the primary concerns, and we appreciate the reviewers’ understanding of these limitations.

Author response image 1.

Figures 2 & 4 represent another example of how deceiving could be a simple comparison of the intensity of fluorescence between the genotypes. It is not clear whether the reduced immunofluorescence of the investigated molecules (ESPN1, EPS8, GNAI3, or FSCN2) results from their mis-localization or represents a simple consequence of the fact that a thinner stereocilium would always have a smaller signal of the protein of interest, even though the ratio of this protein to the number of actin filaments remains unchanged. According to my examination of the representative images of these figures, loss of Srf produces mis-localization of the investigated proteins and irregular labeling in different stereocilia of the same bundle, while loss of Mrtfb does not. Obviously, a simple quantification of the intensity of fluorescence conceals these important differences.

Yes, we agree. In addition to the quantification of tip protein intensity, we have added a few more analyses in the revised Figure 3 and Figure 6, such as the percentage of row 1 tip stereocilia with tip protein staining and the percentage of IHCs with tip protein staining on row 2 tip. Using the results mentioned above, the differences in the expression level, the row-specific distribution and the irregular labeling of tip proteins between the control and the mutants can be analyzed more thoroughly.

Reviewer #2 (Public Review):

The analysis of bundle morphology using both confocal and SEM imaging is a strength of the paper and the authors have some nice images, especially with SEM. Still, the main weakness is that it is unclear how significant their findings are in terms of understanding bundle development; the mouse phenotypes are not distinct enough to make it clear that they serve different functions so the reader is left wondering what the main takeaway is.

Based on the reviewer’s comments, in this revised manuscript, we put more emphasis on describing the effects of SRF and MRTFB on key tip proteins’ localization pattern during stereocilia development, represented by ESPN1, EPS8 and GNAI3, as well as the effects of SRF and MRTFB on the F-actin organization of cuticular plate using TEM. We have made substantial efforts to interpret the mechanistic underpinnings of the roles of SRF and MRTFB in hair cells. This is reflected in the revised Figures 1, 3, 4, 6, and 10, where we provide more comprehensive insights into the mechanisms at play.

We interpret our data in a way that both SRF and MRTF regulate the development and maintenance of the hair cell’s actin cytoskeleton in a complementary manner. Deletion of either gene thus results in somewhat similar phenotypes in hair cell morphology, despite the surprising lack of overlap of SRF and MRTFB downstream targets in the hair cell.

In Figure 1 and 3, changes in bundle morphology clearly don't occur until after P5. Widening still occurs to some extent but lengthening does not and instead the stereocilia appear to shrink in length. EPS8 levels appear to be the most reduced of all the tip proteins (Srf mutants) so I wonder if these mutants are just similar to an EPS8 KO if the loss of EPS8 occurred postnatally (P0-P5).

To address this question, we performed EPS8 staining on the control and Srf cKO hair cells at P4 and P10. We found that the dramatic decrease of the row 1 tip signal for EPS8 started since P4 in Srf cKO IHCs. Although the major hair bundle phenotype of Eps8 KO, including the defects of row 1 stereocilia lengthening and additional rows of short stereocilia also appeared in Srf cKO IHCs, there are still some bundle morphology differences between Eps8 KO and Srf cKO. For example, firstly, both Eps8 KO OHCs and IHCs showed additional rows of short stereocilia, but we only observed additional rows of short stereocilia in Srf cKO IHCs. Secondly, in Valeria Zampini’s study, SEM and TEM images did not show an obvious reduction of row 2 stereocilia widening (P18-P35), while our analysis of SEM images confirmed that the width of row 2 IHC stereocilia was drastically reduced by 40% in Srf cKO (P15). Generally, we think although Srf cKO hair bundles are somewhat similar to Eps8 KO, the Srf cKO hair bundle phenotype might be governed by multiple candidate genes cooperatively.

Reference:

Valeria Zampini, et al. Eps8 regulates hair bundle length and functional maturation of mammalian auditory hair cells. PLoS Biol. 2011 Apr;9(4): e1001048.

A major shortcoming is that there are few details on how the image analyses were done. Were SEM images corrected for shrinkage? How was each of the immunocytochemistry quantitation (e.g., cuticular plates for phalloidin and tip staining for antibodies) done? There are multiple ways of doing this but there are few indications in the manuscript.

We apologize for not making the description of the procedure of images analyses clear enough. As described in Nicolas Grillet group’s study, live and mildly-fixed IHC stereocilia have similar dimensions, while SEM preparation results in a hair bundle at a 2:3 scale compared to the live preparation. In our study, the hair cells selected for SEM imaging and measurements were located in the basal turn (30-32kHz), while the hair cells selected for fluorescence-based imaging and measurements were located in the middle turn (20-24kHz) or the basal turn (32-36kHz). Although our SEM imaging and fluorescence-based imaging of basal turn’s hair bundles were not from the same area exactly, the control hair bundles with SEM imaging have reduced row 1 stereocilia length by 10%-20%, compared to the control hair bundles with fluorescence-based imaging (revised Figure 2 and Figure 5). Generally, our stereocilia dimensions data showed appropriate shrinkage caused by the SEM preparation.

Recognizing the need for clarity, we have provided a detailed description of our image quantification and analysis procedures in the “Materials and Methods” section, specifically under “Immunocytochemistry.” This will aid readers in understanding our methodologies and ensure transparency in our approach.

Reference:

Katharine K Miller, et al. Dimensions of a Living Cochlear Hair Bundle. Front Cell Dev Biol. 2021 Nov 25:9:742529.

The tip protein analysis in Figs 2 and 4 is nice but it would be nice for the authors to show the protein staining separately from the phalloidin so you could see how restricted to the tips it is (each in grayscale). This is especially true for the CNN2 labeling in Fig 7 as it does not look particularly tip specific in the x-y panels. It would be especially important to see the antibody staining in the reslices separate from phalloidin.

Thank you for the suggestions. We have shown tip proteins staining in grayscale separately from the phalloidin in the revised Figure 3 and Figure 6. To clearly show the tip-specific localization of CNN2, we conducted CNN2 staining at different ages during hair bundle development and showed CNN2 labeling in grayscale and in reslices in revised Figure 9-figure supplement 1B.

In Fig 6, why was the transcriptome analysis at P2 given that the phenotype in these mice occurs much later? While redoing the transcriptome analysis is probably not an option, an alternative would be to show more examples of EPS8/GNAI/CNN2 staining in the KO, but at younger ages closer to the time of PCR analysis, such as at P5. Pinpointing when the tip protein intensities start to decrease in the KOs would be useful rather than just showing one age (P10).

We agree with the reviewer. To address this question, we have performed ESPN1, EPS8 and GNAI3 staining on the control and the mutant’s hair cells at P4, P10 and P15 (the revised Figures 3 and 6). According to the new results, we found that the dramatic decreases of the row 1 tip signal for ESPN1 and EPS8 started since P4 in Srf cKO IHCs, is consistent with the appearance of the mild reduction of row 1 stereocilia length in P5 Srf cKO IHCs. For Mrtfb cKO hair cells, the obvious reduction of the row 1 tip signal for ESPN1 was observed until P10. However, a few genes related to cell adhesion and regulation of actin cytoskeleton were significantly down-regulated in P2 Mrtfb deficient hair cell transcriptome. We think that in hair cells the MRTFB may not play a major role in the regulation of stereocilia development, so the morphological defects of stereocilia happened much later in the Mrtfb mutant than in the Srf mutant.

While it is certainly interesting if it turns out CNN2 is indeed at tips in this phase, the experiments do not tell us that much about what role CNN2 may be playing. It is notable that in Fig 7E in the control+GFP panel, CNN2 does not appear to be at the tips. Those images are at P11 whereas the images in panel A are at P6 so perhaps CNN2 decreases after the widening phase. An important missing control is the Anc80L65-Cnn2 AAV in a wild-type cochlea.

We agree with the reviewer. We have conducted more immunostaining experiments to confirm the expression pattern of CNN2 during the stereocilia development, from P0 to P11. The results were included in the revised Figure 9-figure supplement 1B. As the reviewer suggested, CNN2 expression pattern in control cochlea injected with Anc80L65-Cnn2 AAV has also been provided in revised Figure 9E.

Author response:

Reviewer #1 (Public Review):

In this paper, Tompary & Davachi present work looking at how memories become integrated over time in the brain, and relating those mechanisms to responses on a priming task as a behavioral measure of memory linkage. They find that remotely but not recently formed memories are behaviorally linked and that this is associated with a change in the neural representation in mPFC. They also find that the same behavioral outcomes are associated with the increased coupling of the posterior hippocampus with category-sensitive parts of the neocortex (LOC) during a post-learning rest period-again only for remotely learned information. There was also correspondence in rest connectivity (posterior hippocampus-LOC) and representational change (mPFC) such that for remote memories specifically, the initial post-learning connectivity enhancement during rest related to longer-term mPFC representational change.

This work has many strengths. The topic of this paper is very interesting, and the data provide a really nice package in terms of providing a mechanistic account of how memories become integrated over a delay. The paper is also exceptionally well-written and a pleasure to read. There are two studies, including one large behavioral study, and the findings replicate in the smaller fMRI sample. I do however have two fairly substantive concerns about the analytic approach, where more data will be required before we can know whether the interpretations are an appropriate reflection of the findings. These and other concerns are described below.

Thank you for the positive comments! We are proud of this work, and we feel that the paper is greatly strengthened by the revisions we made in response to your feedback. Please see below for specific changes that we’ve made.

1) One major concern relates to the lack of a pre-encoding baseline scan prior to recent learning.

a) First, I think it would be helpful if the authors could clarify why there was no pre-learning rest scan dedicated to the recent condition. Was this simply a feasibility consideration, or were there theoretical reasons why this would be less "clean"? Including this information in the paper would be helpful for context. Apologies if I missed this detail in the paper.

This is a great point and something that we struggled with when developing this experiment. We considered several factors when deciding whether to include a pre-learning baseline on day two. First, the day 2 scan session was longer than that of day 1 because it included the recognition priming and explicit memory tasks, and the addition of a baseline scan would have made the length of the session longer than a typical scan session – about 2 hours in the scanner in total – and we were concerned that participant engagement would be difficult to sustain across a longer session. Second, we anticipated that the pre-learning scan would not have been a ‘clean’ measure of baseline processing, but rather would include signal related to post-learning processing of the day 1 sequences, as multi-variate reactivation of learned stimuli have been observed in rest scans collected 24-hours after learning (Schlichting & Preston, 2014). We have added these considerations to the Discussion (page 39, lines 1047-1070).

b) Second, I was hoping the authors could speak to what they think is reflected in the post-encoding "recent" scan. Is it possible that these data could also reflect the processing of the remote memories? I think, though am not positive, that the authors may be alluding to this in the penultimate paragraph of the discussion (p. 33) when noting the LOC-mPFC connectivity findings. Could there be the reinstatement of the old memories due to being back in the same experimental context and so forth? I wonder the extent to which the authors think the data from this scan can be reflected as strictly reflecting recent memories, particularly given it is relative to the pre-encoding baseline from before the remote memories, as well (and therefore in theory could reflect both the remote + recent). (I should also acknowledge that, if it is the case that the authors think there might be some remote memory processing during the recent learning session in general, a pre-learning rest scan might not have been "clean" either, in that it could have reflected some processing of the remote memories-i.e., perhaps a clean pre-learning scan for the recent learning session related to point 1a is simply not possible.)

We propose that theoretically, the post-learning recent scan could indeed reflect mixture of remote and recent sequences. This is one of the drawbacks of splitting encoding into two sessions rather than combining encoding into one session and splitting retrieval into an immediate and delayed session; any rest scans that are collected on Day 2 may have signal that relates to processing of the Day 1 remote sequences, which is why we decided against the pre-learning baseline for Day 2, as you had noted.

You are correct that we alluded to in our original submission when discussing the LOC-mPFC coupling result, and we have taken steps to discuss this more explicitly. In Brief, we find greater LOC-mPFC connectivity only after recent learning relative to the pre-learning baseline, and cortical-cortical connectivity could be indicative of processing memories that already have undergone some consolidation (Takashima et al., 2009; Smith et al., 2010). From another vantage point, the mPFC representation of Day 1 learning may have led to increased connectivity with LOC on Day 2 due to Day 1 learning beginning to resemble consolidated prior knowledge (van Kesteren et al., 2010). While this effect is consistent with prior literature and theory, it's unclear why we would find evidence of processing of the remote memories and not the recent memories. Furthermore, the change in LOC-mPFC connectivity in this scan did not correlate with memory behaviors from either learning session, which could be because signal from this scan reflects a mix of processing of the two different learning sessions. With these ideas in mind, we have fleshed out the discussion of the post-encoding ‘recent’ scan in the Discussion (page 38-39, lines 1039-1044).

c) Third, I am thinking about how both of the above issues might relate to the authors' findings, and would love to see more added to the paper to address this point. Specifically, I assume there are fluctuations in baseline connectivity profile across days within a person, such that the pre-learning connectivity on day 1 might be different from on day 2. Given that, and the lack of a pre-learning connectivity measure on day 2, it would logically follow that the measure of connectivity change from pre- to post-learning is going to be cleaner for the remote memories. In other words, could the lack of connectivity change observed for the recent scan simply be due to the lack of a within-day baseline? Given that otherwise, the post-learning rest should be the same in that it is an immediate reflection of how connectivity changes as a function of learning (depending on whether the authors think that the "recent" scan is actually reflecting "recent + remote"), it seems odd that they both don't show the same corresponding increase in connectivity-which makes me think it may be a baseline difference. I am not sure if this is what the authors are implying when they talk about how day 1 is most similar to prior investigation on p. 20, but if so it might be helpful to state that directly.

We agree that it is puzzling that we don’t see that hippocampal-LOC connectivity does not also increase after recent learning, equivalently to what we see after remote learning. However, the fact that there is an increase from baseline rest to post-recent rest in mPFC – LOC connectivity suggests that it’s not an issue with baseline, but rather that the post-recent learning scan is reflecting processing of the remote memories (although as a caveat, there is no relationship with priming).

On what is now page 23, we were referring to the notion that the Day 1 procedure (baseline rest, learning, post-learning rest) is the most straightforward replication of past work that finds a relationship between hippocampal-cortical coupling and later memory. In contrast, the Day 2 learning and rest scan are less ‘clean’ of a replication in that they are taking place in the shadow of Day 1 learning. We have clarified this in the Results (page 23, lines 597-598).

d) Fourth and very related to my point 1c, I wonder if the lack of correlations for the recent scan with behavior is interpretable, or if it might just be that this is a noisy measure due to imperfect baseline correction. Do the authors have any data or logic they might be able to provide that could speak to these points? One thing that comes to mind is seeing whether the raw post-learning connectivity values (separately for both recent and remote) show the same pattern as the different scores. However, the authors may come up with other clever ways to address this point. If not, it might be worth acknowledging this interpretive challenge in the Discussion.

We thought of three different approaches that could help us to understand whether the lack of correlations in between coupling and behavior in the recent scan was due to noise. First, we correlated recognition priming with raw hippocampal-LOC coupling separately for pre- and post-learning scans, as in Author response image 1:

Author response image 1.

Note that the post-learning chart depicts the relationship between post-remote coupling and remote priming and between post-recent coupling and recent priming (middle). Essentially, post-recent learning coupling did not relate to priming of recently learned sequences (middle; green) while there remains a trend for a relationship between post-remote coupling and priming for remotely learned sequences (middle; blue). However, the significant relationship between coupling and priming that we reported in the paper (right, blue) is driven both by the initial negative relationship that is observed in the pre-learning scan and the positive relationship in the post-remote learning scan. This highlights the importance of using a change score, as there may be spurious initial relationships between connectivity profiles and to-be-learned information that would then mask any learning- and consolidation-related changes.

We also reasoned that if comparisons between the post-recent learning scan and the baseline scan are noisier than between the post-remote learning and baseline scan, there may be differences in the variance of the change scores across participants, such that changes in coupling from baseline to post-recent rest may be more variable than coupling from baseline to post-remote rest. We conducted F-tests to compare the variance of the change in these two hippocampal-LO correlations and found no reliable difference (ratio of difference: F(22, 22) = 0.811, p = .63).

Finally, we explored whether hippocampal-LOC coupling is more stable across participants if compared across two rest scans within the same imaging session (baseline and post-remote) versus across two scans across two separate sessions (baseline and post-recent). Interestingly, coupling was not reliably correlated across scans in either case (baseline/post-remote: r = 0.03, p = 0.89 Baseline/post-recent: r = 0.07, p = .74).

Finally, we evaluated whether hippocampal-LOC coupling was correlated across different rest scans (see Author response image 2). We reasoned that if such coupling was more correlated across baseline and post-remote scans relative to baseline and post-recent scans, that would indicate a within-session stability of participants’ connectivity profiles. At the same time, less correlation of coupling across baseline and post-recent scans would be an indication of a noisier change measure as the measure would additionally include a change in individuals’ connectivity profile over time. We found that there was no difference in the correlation of hipp-LO coupling is across sessions, and the correlation was not reliably significant for either session (baseline/post-remote: r = 0.03, p = 0.89; baseline/post-recent: r = 0.07, p = .74; difference: Steiger’s t = 0.12, p = 0.9).

Author response image 2.

We have included the raw correlations with priming (page 25, lines 654-661, Supplemental Figure 6) as well as text describing the comparison of variances (page 25, lines 642-653). We did not add the comparison of hippocampal-LOC coupling across scans to the current manuscript, as an evaluation of stability of such coupling in the context of learning and reactivation seems out of scope of the current focus of the experiment, but we find this result to be worthy of follow-up in future work.

In summary, further analysis of our data did not reveal any indication that a comparison of rest connectivity across scan sessions inserted noise into the change score between baseline and post-recent learning scans. However, these analyses cannot fully rule that possibility out, and the current analyses do not provide concrete evidence that the post-recent learning scan comprises signals that are a mixture of processing of recent and remote sequences. We discuss these drawbacks in the Discussion (page 39, lines 1047-1070).

2) My second major concern is how the authors have operationalized integration and differentiation. The pattern similarity analysis uses an overall correspondence between the neural similarity and a predicted model as the main metric. In the predicted model, C items that are indirectly associated are more similar to one another than they are C items that are entirely unrelated. The authors are then looking at a change in correspondence (correlation) between the neural data and that prediction model from pre- to post-learning. However, a change in the degree of correspondence with the predicted matrix could be driven by either the unrelated items becoming less similar or the related ones becoming more similar (or both!). Since the interpretation in the paper focuses on change to indirectly related C items, it would be important to report those values directly. For instance, as evidence of differentiation, it would be important to show that there is a greater decrease in similarity for indirectly associated C items than it is for unrelated C items (or even a smaller increase) from pre to post, or that C items that are indirectly related are less similar than are unrelated C items post but not pre-learning. Performing this analysis would confirm that the pattern of results matches the authors' interpretation. This would also impact the interpretation of the subsequent analyses that involve the neural integration measures (e.g., correlation analyses like those on p. 16, which may or may not be driven by increased similarity among overlapping C pairs). I should add that given the specificity to the remote learning in mPFC versus recent in LOC and anterior hippocampus, it is clearly the case that something interesting is going on. However, I think we need more data to understand fully what that "something" is.

We recognize the importance of understanding whether model fits (and changes to them) are driven by similarity of overlapping pairs or non-overlapping pairs. We have modified all figures that visualize model fits to the neural integration model to separately show fits for pre- and post-learning (Figure 3 for mPFC, Supp. Figure 5 for LOC, Supp. Figure 9 for AB similarity in anterior hippocampus & LOC). We have additionally added supplemental figures to show the complete breakdown of similarity each region in a 2 (pre/post) x 2 (overlapping/non-overlapping sequence) x 2 (recent/remote) chart. We decided against including only these latter charts rather than the model fits since the model fits strike a good balance between information and readability. We have also modified text in various sections to focus on these new results.

In brief, the decrease in model fit for mPFC for the remote sequences was driven primarily by a decrease in similarity for the overlapping C items and not the non-overlapping ones (Supplementary Figure 3, page 18, lines 468-472).

Interestingly, in LOC, all C items grew more similar after learning, regardless of their overlap or learning session, but the increase in model fit for C items in the recent condition was driven by a larger increase in similarity for overlapping pairs relative to non-overlapping ones (Supp. Figure 5, page 21, lines 533-536).

We also visualized AB similarity in the anterior hippocampus and LOC in a similar fashion (Supplementary Figure 9).

We have also edited the Methods sections with updated details of these analyses (page 52, lines 1392-1397). We think that including these results considerably strengthen our claims and we are pleased to have them included.

3) The priming task occurred before the post-learning exposure phase and could have impacted the representations. More consideration of this in the paper would be useful. Most critically, since the priming task involves seeing the related C items back-to-back, it would be important to consider whether this experience could have conceivably impacted the neural integration indices. I believe it never would have been the case that unrelated C items were presented sequentially during the priming task, i.e., that related C items always appeared together in this task. I think again the specificity of the remote condition is key and perhaps the authors can leverage this to support their interpretation. Can the authors consider this possibility in the Discussion?

It's true that only C items from the same sequence were presented back-to-back during the priming task, and that this presentation may interfere with observations from the post-learning exposure scan that followed it. We agree that it is worth considering this caveat and have added language in the Discussion (page 40, lines 1071-1086). When designing the study, we reasoned that it was more important for the behavioral priming task to come before the exposure scans, as all items were shown only once in that task, whereas they were shown 4-5 times in a random order in the post-learning exposure phase. Because of this difference in presentation times, and because behavioral priming findings tend to be very sensitive, we concluded that it was more important to protect the priming task from the exposure scan instead of the reverse.

We reasoned, however, that the additional presentation of the C items in the recognition priming task would not substantially override the sequence learning, as C items were each presented 16 times in their sequence (ABC1 and ABC2 16 times each). Furthermore, as this reviewer suggests, the order of C items during recognition was the same for recent and remote conditions, so the fact that we find a selective change in neural representation for the remote condition and don’t also see that change for the recent condition is additional assurance that the recognition priming order did not substantially impact the representations.

4) For the priming task, based on the Figure 2A caption it seems as though every sequence contributes to both the control and primed conditions, but (I believe) this means that the control transition always happens first (and they are always back-to-back). Is this a concern? If RTs are changing over time (getting faster), it would be helpful to know whether the priming effects hold after controlling for trial numbers. I do not think this is a big issue because if it were, you would not expect to see the specificity of the remotely learned information. However, it would be helpful to know given the order of these conditions has to be fixed in their design.

This is a correct understanding of the trial orders in the recognition priming task. We chose to involve the baseline items in the control condition to boost power – this way, priming of each sequence could be tested, while only presenting each item once in this task, as repetition in the recognition phase would have further facilitated response times and potentially masked any priming effects. We agree that accounting for trial order would be useful here, so we ran a mixed-effects linear model to examine responses times both as a function of trial number and of priming condition (primed/control). While there is indeed a large effect of trial number such that participants got faster over time, the priming effect originally observed in the remote condition still holds at the same time. We now report this analysis in the Results section (page 14, lines 337-349 for Expt 1 and pages 14-15, lines 360-362 for Expt 2).

5) The authors should be cautious about the general conclusion that memories with overlapping temporal regularities become neurally integrated - given their findings in MPFC are more consistent with overall differentiation (though as noted above, I think we need more data on this to know for sure what is going on).

We realize this conclusion was overly simplistic and, in several places, have revised the general conclusions to be more specific about the nuanced similarity findings.

6) It would be worth stating a few more details and perhaps providing additional logic or justification in the main text about the pre- and post-exposure phases were set up and why. How many times each object was presented pre and post, and how the sequencing was determined (were any constraints put in place e.g., such that C1 and C2 did not appear close in time?). What was the cover task (I think this is important to the interpretation & so belongs in the main paper)? Were there considerations involving the fact that this is a different sequence of the same objects the participants would later be learning - e.g., interference, etc.?

These details can be found in the Methods section (pages 50-51, lines 1337-1353) and we’ve added a new summary of that section in the Results (page 17, lines 424- 425 and 432-435). In brief, a visual hash tag appeared on a small subset of images and participants pressed a button when this occurred, and C1 and C2 objects were presented in separate scans (as were A and B objects) to minimize inflated neural similarity due to temporal proximity.

Reviewer #2 (Public Review):

The manuscript by Tompary & Davachi presents results from two experiments, one behavior only and one fMRI plus behavior. They examine the important question of how to separate object memories (C1 and C2) that are never experienced together in time and become linked by shared predictive cues in a sequence (A followed by B followed by one of the C items). The authors developed an implicit priming task that provides a novel behavioral metric for such integration. They find significant C1-C2 priming for sequences that were learned 24h prior to the test, but not for recently learned sequences, suggesting that associative links between the two originally separate memories emerge over an extended period of consolidation. The fMRI study relates this behavioral integration effect to two neural metrics: pattern similarity changes in the medial prefrontal cortex (mPFC) as a measure of neural integration, and changes in hippocampal-LOC connectivity as a measure of post-learning consolidation. While fMRI patterns in mPFC overall show differentiation rather than integration (i.e., C1-C2 representational distances become larger), the authors find a robust correlation such that increasing pattern similarity in mPFC relates to stronger integration in the priming test, and this relationship is again specific to remote memories. Moreover, connectivity between the posterior hippocampus and LOC during post-learning rest is positively related to the behavioral integration effect as well as the mPFC neural similarity index, again specifically for remote memories. Overall, this is a coherent set of findings with interesting theoretical implications for consolidation theories, which will be of broad interest to the memory, learning, and predictive coding communities.

Strengths:

1) The implicit associative priming task designed for this study provides a promising new tool for assessing the formation of mnemonic links that influence behavior without explicit retrieval demands. The authors find an interesting dissociation between this implicit measure of memory integration and more commonly used explicit inference measures: a priming effect on the implicit task only evolved after a 24h consolidation period, while the ability to explicitly link the two critical object memories is present immediately after learning. While speculative at this point, these two measures thus appear to tap into neocortical and hippocampal learning processes, respectively, and this potential dissociation will be of interest to future studies investigating time-dependent integration processes in memory.

2) The experimental task is well designed for isolating pre- vs post-learning changes in neural similarity and connectivity, including important controls of baseline neural similarity and connectivity.

3) The main claim of a consolidation-dependent effect is supported by a coherent set of findings that relate behavioral integration to neural changes. The specificity of the effects on remote memories makes the results particularly interesting and compelling.

4) The authors are transparent about unexpected results, for example, the finding that overall similarity in mPFC is consistent with a differentiation rather than an integration model.

Thank you for the positive comments!

Weaknesses:

1) The sequence learning and recognition priming tasks are cleverly designed to isolate the effects of interest while controlling for potential order effects. However, due to the complex nature of the task, it is difficult for the reader to infer all the transition probabilities between item types and how they may influence the behavioral priming results. For example, baseline items (BL) are interspersed between repeated sequences during learning, and thus presumably can only occur before an A item or after a C item. This seems to create non-random predictive relationships such that C is often followed by BL, and BL by A items. If this relationship is reversed during the recognition priming task, where the sequence is always BL-C1-C2, this violation of expectations might slow down reaction times and deflate the baseline measure. It would be helpful if the manuscript explicitly reported transition probabilities for each relevant item type in the priming task relative to the sequence learning task and discussed how a match vs mismatch may influence the observed priming effects.

We have added a table of transition probabilities across the learning, recognition priming, and exposure scans (now Table 1, page 48). We have also included some additional description of the change in transition probabilities across different tasks in the Methods section. Specifically, if participants are indeed learning item types and rules about their order, then both the control and the primed conditions would violate that order. Since C1 and C2 items never appeared together, viewing C1 would give rise to an expectation of seeing a BL item, which would also be violated. This suggests that our priming effects are driven by sequence-specific relationships rather than learning of the probabilities of different item types. We’ve added this consideration to the Methods section (page 45, lines 1212-1221).

Another critical point to consider (and that the transition probabilities do not reflect) is that during learning, while C is followed either by A or BL, they are followed by different A or BL items. In contrast, a given A is always followed by the same B object, which is always followed by one of two C objects. While the order of item types is semi-predictable, the order of objects (specific items) themselves are not. This can be seen in the response times during learning, such that response times for A and BL items are always slower than for B and C items. We have explained this nuance in the figure text for Table 1.

2) The choice of what regions of interest to include in the different sets of analyses could be better motivated. For example, even though briefly discussed in the intro, it remains unclear why the posterior but not the anterior hippocampus is of interest for the connectivity analyses, and why the main target is LOC, not mPFC, given past results including from this group (Tompary & Davachi, 2017). Moreover, for readers not familiar with this literature, it would help if references were provided to suggest that a predictable > unpredictable contrast is well suited for functionally defining mPFC, as done in the present study.

We have clarified our reasoning for each of these choices throughout the manuscript and believe that our logic is now much more transparent. For an expanded reasoning of why we were motivated to look at posterior and not anterior hippocampus, see pages 6-7, lines 135-159, and our response to R2. In brief, past research focusing on post-encoding connectivity with the hippocampus suggests that posterior aspect is more likely to couple with category-selective cortex after learning neutral, non-rewarded objects much like the stimuli used in the present study.

We also clarify our reasoning for LOC over mPFC. While theoretically, mPFC is thought to be a candidate region for coupling with the hippocampus during consolidation, the bulk of empirical work to date has revealed post-encoding connectivity between the hippocampus and category-selective cortex in the ventral and occipital lobes (page 6, lines 123-134).

As for the use of the predictable > unpredictable contrast for functionally defining cortical regions, we reasoned that cortical regions that were sensitive to the temporal regularities generated by the sequences may be further involved in their offline consolidation and long-term storage (Danker & Anderson, 2010; Davachi & Danker, 2013; McClelland et al., 1995). We have added this justification to the Methods section (page 18, lines 454-460).

3) Relatedly, multiple comparison corrections should be applied in the fMRI integration and connectivity analyses whenever the same contrast is performed on multiple regions in an exploratory manner.

We now correct for multiple comparisons using Bonferroni correction, and this correction depends on the number of regions in which each analysis is conducted. Please see page 55, lines 1483-1490, in the Methods section for details of each analysis.

Reviewer #3 (Public Review):

The authors of this manuscript sought to illuminate a link between a behavioral measure of integration and neural markers of cortical integration associated with systems consolidation (post-encoding connectivity, change in representational neural overlap). To that aim, participants incidentally encoded sequences of objects in the fMRI scanner. Unbeknownst to participants, the first two objects of the presented ABC triplet sequences overlapped for a given pair of sequences. This allowed the authors to probe the integration of unique C objects that were never directly presented in the same sequence, but which shared the same preceding A and B objects. They encoded one set of objects on Day 1 (remote condition), another set of objects 24 hours later (recent condition) and tested implicit and explicit memory for the learned sequences on Day 2. They additionally collected baseline and post-encoding resting-state scans. As their measure of behavioral integration, the authors examined reaction time during an Old/New judgement task for C objects depending on if they were preceded by a C object from an overlapping sequence (primed condition) versus a baseline object. They found faster reaction times for the primed objects compared to the control condition for remote but not recently learned objects, suggesting that the C objects from overlapping sequences became integrated over time. They then examined pattern similarity in a priori ROIs as a measure of neural integration and found that participants showing evidence of integration of C objects from overlapping sequences in the medial prefrontal cortex for remotely learned objects also showed a stronger implicit priming effect between those C objects over time. When they examined the change in connectivity between their ROIs after encoding, they also found that connectivity between the posterior hippocampus and lateral occipital cortex correlated with larger priming effects for remotely learned objects, and that lateral occipital connectivity with the medial prefrontal cortex was related to neural integration of remote objects from overlapping sequences.

The authors aim to provide evidence of a relationship between behavioral and neural measures of integration with consolidation is interesting, important, and difficult to achieve given the longitudinal nature of studies required to answer this question. Strengths of this study include a creative behavioral task, and solid modelling approaches for fMRI data with careful control for several known confounds such as bold activation on pattern analysis results, motion, and physiological noise. The authors replicate their behavioral observations across two separate experiments, one of which included a large sample size, and found similar results that speak to the reliability of the observed behavioral phenomenon. In addition, they document several correlations between neural measures and task performance, lending functional significance to their neural findings.

Thank you for this positive assessment of our study!

However, this study is not without notable weaknesses that limit the strength of the manuscript. The authors report a behavioral priming effect suggestive of integration of remote but not recent memories, leading to the interpretation that the priming effect emerges with consolidation. However, they did not observe a reliable interaction between the priming condition and learning session (recent/remote) on reaction times, meaning that the priming effect for remote memories was not reliably greater than that observed for recent. In addition, the emergence of a priming effect for remote memories does not appear to be due to faster reaction times for primed targets over time (the condition of interest), but rather, slower reaction times for control items in the remote condition compared to recent. These issues limit the strength of the claim that the priming effect observed is due to C items of interest being integrated in a consolidation-dependent manner.

We acknowledge that the lack of a day by condition interaction in the behavioral priming effect should discussed and now discuss this data in a more nuanced manner. While it’s true that the priming effect emerges due to a slowing of the control items over time, this slowing is consistent with classic time-dependent effects demonstrating slower response times for more delayed memories. The fact that the response times in the primed condition does not show this slowing can be interpreted as a protection against this slowing that would otherwise occur. Please see page 29, lines 758-766, for this added discussion.

Similarly, the interactions between neural variables of interest and learning session needed to strongly show a significant consolidation-related effect in the brain were sometimes tenuous. There was no reliable difference in neural representational pattern analysis fit to a model of neural integration between the short and long delays in the medial prefrontal cortex or lateral occipital cortex, nor was the posterior hippocampus-lateral occipital cortex post-encoding connectivity correlation with subsequent priming significantly different for recent and remote memories. While the relationship between integration model fit in the medial prefrontal cortex and subsequent priming (which was significantly different from that occurring for recent memories) was one of the stronger findings of the paper in favor of a consolidation-related effect on behavior, is it possible that lack of a behavioral priming effect for recent memories due to possible issues with the control condition could mask a correlation between neural and behavioral integration in the recent memory condition?

While we acknowledge that lack of a statistically reliable interaction between neural measures and behavioral priming in many cases, we are heartened by the reliable difference in the relationship between mPFC similarity and priming over time, which was our main planned prediction. In addition to adding caveats in the discussion about the neural measures and behavioral findings in the recent condition (see our response to R1.1 and R1.4 for more details), we have added language throughout the manuscript noting the need to interpret these data with caution.

These limitations are especially notable when one considers that priming does not classically require a period of prolonged consolidation to occur, and prominent models of systems consolidation rather pertain to explicit memory. While the authors have provided evidence that neural integration in the medial prefrontal cortex, as well as post-encoding coupling between the lateral occipital cortex and posterior hippocampus, are related to faster reaction times for primed objects of overlapping sequences compared to their control condition, more work is needed to verify that the observed findings indeed reflect consolidation dependent integration as proposed.

We agree that more work is needed to provide converging evidence for these novel findings. However, we wish to counter the notion that systems consolidation models are relevant only for explicit memories. Although models of systems consolidation often mention transformations from episodic to semantic memory, the critical mechanisms that define the models involve changes in the neural ensembles of a memory that is initially laid down in the hippocampus and is taught to cortex over time. This transformation of neural traces is not specific to explicit/declarative forms of memory. For example, implicit statistical learning initially depends on intact hippocampal function (Schapiro et al., 2014) and improves over consolidation (Durrant et al., 2011, 2013; Kóbor et al., 2017).

Second, while there are many classical findings of priming during or immediately after learning, there are several instances of priming used to measure consolidation-related changes to newly learned information. For instance, priming has been used as a measure of lexical integration, demonstrating that new word learning benefits from a night of sleep (Wang et al., 2017; Gaskell et al., 2019) or a 1-week delay (Tamminen & Gaskell, 2013). The issue is not whether priming can occur immediately, it is whether priming increases with a delay.

Finally, it is helpful to think about models of memory systems that divide memory representations not by their explicit/implicit nature, but along other important dimensions such as their neural bases, their flexibility vs rigidity, and their capacity for rapid vs slow learning (Henke, 2010). Considering this evidence, we suggest that systems consolidation models are most useful when considering how transformations in the underlying neural memory representation affects its behavioral expression, rather than focusing on the extent that the memory representation is explicit or implicit.

With all this said, we have added text to the discussion reminding the reader that there was no statistically significant difference in priming as a function of the delay (page 29, lines 764 - 766). However, we are encouraged by the fact that the relationship between priming and mPFC neural similarity was significantly stronger for remotely learned objects relative to recently learned ones, as this is directly in line with systems consolidation theories.

References

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Author Response

Reviewer #1 (Public Review):

This study used a multi-day learning paradigm combined with fMRI to reveal neural changes reflecting the learning of new (arbitrary) shape-sound associations. In the scanner, the shapes and sounds are presented separately and together, both before and after learning. When they are presented together, they can be either consistent or inconsistent with the learned associations. The analyses focus on auditory and visual cortices, as well as the object-selective cortex (LOC) and anterior temporal lobe regions (temporal pole (TP) and perirhinal cortex (PRC)). Results revealed several learning-induced changes, particularly in the anterior temporal lobe regions. First, the LOC and PRC showed a reduced bias to shapes vs sounds (presented separately) after learning. Second, the TP responded more strongly to incongruent than congruent shape-sound pairs after learning. Third, the similarity of TP activity patterns to sounds and shapes (presented separately) was increased for non-matching shape-sound comparisons after learning. Fourth, when comparing the pattern similarity of individual features to combined shape-sound stimuli, the PRC showed a reduced bias towards visual features after learning. Finally, comparing patterns to combined shape-sound stimuli before and after learning revealed a reduced (and negative) similarity for incongruent combinations in PRC. These results are all interpreted as evidence for an explicit integrative code of newly learned multimodal objects, in which the whole is different from the sum of the parts.

The study has many strengths. It addresses a fundamental question that is of broad interest, the learning paradigm is well-designed and controlled, and the stimuli are real 3D stimuli that participants interact with. The manuscript is well written and the figures are very informative, clearly illustrating the analyses performed.

There are also some weaknesses. The sample size (N=17) is small for detecting the subtle effects of learning. Most of the statistical analyses are not corrected for multiple comparisons (ROIs), and the specificity of the key results to specific regions is also not tested. Furthermore, the evidence for an integrative representation is rather indirect, and alternative interpretations for these results are not considered.

We thank the reviewer for their careful reading and the positive comments on our manuscript. As suggested, we have conducted additional analyses of theoretically-motivated ROIs and have found that temporal pole and perirhinal cortex are the only regions to show the key experience-dependent transformations. We are much more cautious with respect to multiple comparisons, and have removed a series of post hoc across-ROI comparisons that were irrelevant to the key questions of the present manuscript. The revised manuscript now includes much more discussion about alternative interpretations as suggested by the reviewer (and also by the other reviewers).

Additionally, we looked into scanning more participants, but our scanner has since had a full upgrade and the sequence used in the current study is no longer supported by our scanner. However, we note that while most analyses contain 17 participants, we employed a within-subject learning design that is not typically used in fMRI experiments and increases our power to detect an effect. This is supported by the robust effect size of the behavioural data, whereby 17 out of 18 participants revealed a learning effect (Cohen’s D = 1.28) and which was replicated in a follow-up experiment with a larger sample size.

We address the other reviewer comments point-by-point in the below.

Reviewer #2 (Public Review):

Li et al. used a four-day fMRI design to investigate how unimodal feature information is combined, integrated, or abstracted to form a multimodal object representation. The experimental question is of great interest and understanding how the human brain combines featural information to form complex representations is relevant for a wide range of researchers in neuroscience, cognitive science, and AI. While most fMRI research on object representations is limited to visual information, the authors examined how visual and auditory information is integrated to form a multimodal object representation. The experimental design is elegant and clever. Three visual shapes and three auditory sounds were used as the unimodal features; the visual shapes were used to create 3D-printed objects. On Day 1, the participants interacted with the 3D objects to learn the visual features, but the objects were not paired with the auditory features, which were played separately. On Day 2, participants were scanned with fMRI while they were exposed to the unimodal visual and auditory features as well as pairs of visual-auditory cues. On Day 3, participants again interacted with the 3D objects but now each was paired with one of the three sounds that played from an internal speaker. On Day 4, participants completed the same fMRI scanning runs they completed on Day 2, except now some visual-auditory feature pairs corresponded with Congruent (learned) objects, and some with Incongruent (unlearned) objects. Using the same fMRI design on Days 2 and 4 enables a well-controlled comparison between feature- and object-evoked neural representations before and after learning. The notable results corresponded to findings in the perirhinal cortex and temporal pole. The authors report (1) that a visual bias on Day 2 for unimodal features in the perirhinal cortex was attenuated after learning on Day 4, (2) a decreased univariate response to congruent vs. incongruent visual-auditory objects in the temporal pole on Day 4, (3) decreased pattern similarity between congruent vs. incongruent pairs of visual and auditory unimodal features in the temporal pole on Day 4, (4) in the perirhinal cortex, visual unimodal features on Day 2 do not correlate with their respective visual-auditory objects on Day 4, and (5) in the perirhinal cortex, multimodal object representations across Days 2 and 4 are uncorrelated for congruent objects and anticorrelated for incongruent. The authors claim that each of these results supports the theory that multimodal objects are represented in an "explicit integrative" code separate from feature representations. While these data are valuable and the results are interesting, the authors' claims are not well supported by their findings.

We thank the reviewer for the careful reading of our manuscript and positive comments. Overall, we now stay closer to the data when describing the results and provide our interpretation of these results in the discussion section while remaining open to alternative interpretations (as also suggested by Reviewer 1).

(1) In the introduction, the authors contrast two theories: (a) multimodal objects are represented in the co-activation of unimodal features, and (b) multimodal objects are represented in an explicit integrative code such that the whole is different than the sum of its parts. However, the distinction between these two theories is not straightforward. An explanation of what is precisely meant by "explicit" and "integrative" would clarify the authors' theoretical stance. Perhaps we can assume that an "explicit" representation is a new representation that is created to represent a multimodal object. What is meant by "integrative" is more ambiguous-unimodal features could be integrated within a representation in a manner that preserves the decodability of the unimodal features, or alternatively the multimodal representation could be completely abstracted away from the constituent features such that the features are no longer decodable. Even if the object representation is "explicit" and distinct from the unimodal feature representations, it can in theory still contain featural information, though perhaps warped or transformed. The authors do not clearly commit to a degree of featural abstraction in their theory of "explicit integrative" multimodal object representations which makes it difficult to assess the validity of their claims.

Due to its ambiguity, we removed the term “explicit” and now make it clear that our central question was whether crossmodal object representations require only unimodal feature-level representations (e.g., frogs are created from only the combination of shape and sound) or whether crossmodal object representations also rely on an integrative code distinct from the unimodal features (e.g., there is something more to “frog” than its original shape and sound). We now clarify this in the revised manuscript.

“One theoretical view from the cognitive sciences suggests that crossmodal objects are built from component unimodal features represented across distributed sensory regions.8 Under this view, when a child thinks about “frog”, the visual cortex represents the appearance of the shape of the frog whereas the auditory cortex represents the croaking sound. Alternatively, other theoretical views predict that multisensory objects are not only built from their component unimodal sensory features, but that there is also a crossmodal integrative code that is different from the sum of these parts.9,10,11,12,13 These latter views propose that anterior temporal lobe structures can act as a polymodal “hub” that combines separate features into integrated wholes.9,11,14,15” – pg. 4

For this reason, we designed our paradigm to equate the unimodal representations, such that neural differences between the congruent and incongruent conditions provide evidence for a crossmodal integrative code different from the unimodal features (because the unimodal features are equated by default in the design).

“Critically, our four-day learning task allowed us to isolate any neural activity associated with integrative coding in anterior temporal lobe structures that emerges with experience and differs from the neural patterns recorded at baseline. The learned and non-learned crossmodal objects were constructed from the same set of three validated shape and sound features, ensuring that factors such as familiarity with the unimodal features, subjective similarity, and feature identity were tightly controlled (Figure 2). If the mind represented crossmodal objects entirely as the reactivation of unimodal shapes and sounds (i.e., objects are constructed from their parts), then there should be no difference between the learned and non-learned objects (because they were created from the same three shapes and sounds). By contrast, if the mind represented crossmodal objects as something over and above their component features (i.e., representations for crossmodal objects rely on integrative coding that is different from the sum of their parts), then there should be behavioral and neural differences between learned and non-learned crossmodal objects (because the only difference across the objects is the learned relationship between the parts). Furthermore, this design allowed us to determine the relationship between the object representation acquired after crossmodal learning and the unimodal feature representations acquired before crossmodal learning. That is, we could examine whether learning led to abstraction of the object representations such that it no longer resembled the unimodal feature representations.” – pg. 5

Furthermore, we agree with the reviewer that our definition and methodological design does not directly capture the structure of the integrative code. With experience, the unimodal feature representations may be completely abstracted away, warped, or changed in a nonlinear transformation. We suggest that crossmodal learning forms an integrative code that is different from the original unimodal representations in the anterior temporal lobes, however, we agree that future work is needed to more directly capture the structure of the integrative code that emerges with experience.

“In our task, participants had to differentiate congruent and incongruent objects constructed from the same three shape and sound features (Figure 2). An efficient way to solve this task would be to form distinct object-level outputs from the overlapping unimodal feature-level inputs such that congruent objects are made to be orthogonal from the representations before learning (i.e., measured as pattern similarity equal to 0 in the perirhinal cortex; Figure 5b, 6, Supplemental Figure S5), whereas non-learned incongruent objects could be made to be dissimilar from the representations before learning (i.e., anticorrelation, measured as patten similarity less than 0 in the perirhinal cortex; Figure 6). Because our paradigm could decouple neural responses to the learned object representations (on Day 4) from the original component unimodal features at baseline (on Day 2), these results could be taken as evidence of pattern separation in the human perirhinal cortex.11,12 However, our pattern of results could also be explained by other types of crossmodal integrative coding. For example, incongruent object representations may be less stable than congruent object representations, such that incongruent objects representation are warped to a greater extent than congruent objects (Figure 6).” – pg. 18

“As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation.” – pg. 18

(2) After participants learned the multimodal objects, the authors report a decreased univariate response to congruent visual-auditory objects relative to incongruent objects in the temporal pole. This is claimed to support the existence of an explicit, integrative code for multimodal objects. Given the number of alternative explanations for this finding, this claim seems unwarranted. A simpler interpretation of these results is that the temporal pole is responding to the novelty of the incongruent visual-auditory objects. If there is in fact an explicit, integrative multimodal object representation in the temporal pole, it is unclear why this would manifest in a decreased univariate response.

We thank the reviewer for identifying this issue. Our behavioural design controls unimodal feature-level novelty but allows object-level novelty to differ. Thus, neural differences between the congruent and incongruent conditions reflects sensitivity to the object-level differences between the combination of shape and sound. However, we agree that there are multiple interpretations regarding the nature of how the integrative code is structured in the temporal pole and perirhinal cortex. We have removed the interpretation highlighted by the reviewer from the results. Instead, we now provide our preferred interpretation in the discussion, while acknowledging the other possibilities that the reviewer mentions.

As one possibility, these results in temporal pole may reflect “conceptual combination”. “hummingbird” – a congruent pairing – may require less neural resources than an incongruent pairing such as “bark-frog”.

“Furthermore, these distinct anterior temporal lobe structures may be involved with integrative coding in different ways. For example, the crossmodal object representations measured after learning were found to be related to the component unimodal feature representations measured before learning in the temporal pole but not the perirhinal cortex (Figure 5, 6, Supplemental Figure S5). Moreover, pattern similarity for congruent shape-sound pairs were lower than the pattern similarity for incongruent shape-sound pairs after crossmodal learning in the temporal pole but not the perirhinal cortex (Figure 4b, Supplemental Figure S3a). As one interpretation of this pattern of results, the temporal pole may represent new crossmodal objects by combining previously learned knowledge. 8,9,10,11,13,14,15,33 Specifically, research into conceptual combination has linked the anterior temporal lobes to compound object concepts such as “hummingbird”.34,35,36 For example, participants during our task may have represented the sound-based “humming” concept and visually-based “bird” concept on Day 1, forming the crossmodal “hummingbird” concept on Day 3; Figure 1, 2, which may recruit less activity in temporal pole than an incongruent pairing such as “barking-frog”. For these reasons, the temporal pole may form a crossmodal object code based on pre-existing knowledge, resulting in reduced neural activity (Figure 3d) and pattern similarity towards features associated with learned objects (Figure 4b).”– pg. 18

(3) The authors ran a neural pattern similarity analysis on the unimodal features before and after multimodal object learning. They found that the similarity between visual and auditory features that composed congruent objects decreased in the temporal pole after multimodal object learning. This was interpreted to reflect an explicit integrative code for multimodal objects, though it is not clear why. First, behavioral data show that participants reported increased similarity between the visual and auditory unimodal features within congruent objects after learning, the opposite of what was found in the temporal pole. Second, it is unclear why an analysis of the unimodal features would be interpreted to reflect the nature of the multimodal object representations. Since the same features corresponded with both congruent and incongruent objects, the nature of the feature representations cannot be interpreted to reflect the nature of the object representations per se. Third, using unimodal feature representations to make claims about object representations seems to contradict the theoretical claim that explicit, integrative object representations are distinct from unimodal features. If the learned multimodal object representation exists separately from the unimodal feature representations, there is no reason why the unimodal features themselves would be influenced by the formation of the object representation. Instead, these results seem to more strongly support the theory that multimodal object learning results in a transformation or warping of feature space.

We apologize for the lack of clarity. We have now overhauled this aspect of our manuscript in an attempt to better highlight key aspects of our experimental design. In particular, because the unimodal features composing the congruent and incongruent objects were equated, neural differences between these conditions would provide evidence for an experience-dependent crossmodal integrative code that is different from its component unimodal features.

Related to the second and third points, we were looking at the extent to which the original unimodal representations change with crossmodal learning. Before crossmodal learning, we found that the perirhinal cortex tracked the similarity between the individual visual shape features and the crossmodal objects that were composed of those visual shapes – however, there was no evidence that perirhinal cortex was tracking the unimodal sound features on those crossmodal objects. After crossmodal learning, we see that this visual shape bias in perirhinal cortex was no longer present – that is, the representation in perirhinal cortex started to look less like the visual features that comprise the objects. Thus, crossmodal learning transformed the perirhinal representations so that they were no longer predominantly grounded in a single visual modality, which may be a mechanism by which object concepts gain their abstraction. We have now tried to be clearer about this interpretation throughout the paper.

Notably, we suggest that experience may change both the crossmodal object representations, as well as the unimodal feature representations. For example, we have previously shown that unimodal visual features are influenced by experience in parallel with the representation of the conjunction (e.g., Liang et al., 2020; Cerebral Cortex). Nevertheless, we remain open to the myriad possible structures of the integrative code that might emerge with experience.

We now clarify these points throughout the manuscript. For example:

“We then examined whether the original representations would change after participants learned how the features were paired together to make specific crossmodal objects, conducting the same analysis described above after crossmodal learning had taken place (Figure 5b). With this analysis, we sought to measure the relationship between the representation for the learned crossmodal object and the original baseline representation for the unimodal features. More specifically, the voxel-wise activity for unimodal feature runs before crossmodal learning was correlated to the voxel-wise activity for crossmodal object runs after crossmodal learning (Figure 5b). Another linear mixed model which included modality as a fixed factor within each ROI revealed that the perirhinal cortex was no longer biased towards visual shape after crossmodal learning (F1,32 = 0.12, p = 0.73), whereas the temporal pole, LOC, V1, and A1 remained biased towards either visual shape or sound (F1,30-32 between 16.20 and 73.42, all p < 0.001, η2 between 0.35 and 0.70).” – pg. 14

“To investigate this effect in perirhinal cortex more specifically, we conducted a linear mixed model to directly compare the change in the visual bias of perirhinal representations from before crossmodal learning to after crossmodal learning (green regions in Figure 5a vs. 5b). Specifically, the linear mixed model included learning day (before vs. after crossmodal learning) and modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object). Results revealed a significant interaction between learning day and modality in the perirhinal cortex (F1,775 = 5.56, p = 0.019, η2 = 0.071), meaning that the baseline visual shape bias observed in perirhinal cortex (green region of Figure 5a) was significantly attenuated with experience (green region of Figure 5b). After crossmodal learning, a given shape no longer invoked significant pattern similarity between objects that had the same shape but differed in terms of what they sounded like. Taken together, these results suggest that prior to learning the crossmodal objects, the perirhinal cortex had a default bias toward representing the visual shape information and was not representing sound information of the crossmodal objects. After crossmodal learning, however, the visual shape bias in perirhinal cortex was no longer present. That is, with crossmodal learning, the representations within perirhinal cortex started to look less like the visual features that comprised the crossmodal objects, providing evidence that the perirhinal representations were no longer predominantly grounded in the visual modality.” – pg. 13

“Importantly, the initial visual shape bias observed in the perirhinal cortex was attenuated by experience (Figure 5, Supplemental Figure S5), suggesting that the perirhinal representations had become abstracted and were no longer predominantly grounded in a single modality after crossmodal learning. One possibility may be that the perirhinal cortex is by default visually driven as an extension to the ventral visual stream,10,11,12 but can act as a polymodal “hub” region for additional crossmodal input following learning.” – pg. 19

(4) The most compelling evidence the authors provide for their theoretical claims is the finding that, in the perirhinal cortex, the unimodal feature representations on Day 2 do not correlate with the multimodal objects they comprise on Day 4. This suggests that the learned multimodal object representations are not combinations of their unimodal features. If unimodal features are not decodable within the congruent object representations, this would support the authors' explicit integrative hypothesis. However, the analyses provided do not go all the way in convincing the reader of this claim. First, the analyses reported do not differentiate between congruent and incongruent objects. If this result in the perirhinal cortex reflects the formation of new multimodal object representations, it should only be true for congruent objects but not incongruent objects. Since the analyses combine congruent and incongruent objects it is not possible to know whether this was the case. Second, just because feature representations on Day 2 do not correlate with multimodal object patterns on Day 4 does not mean that the object representations on Day 4 do not contain featural information. This could be directly tested by correlating feature representations on Day 4 with congruent vs. incongruent object representations on Day 4. It could be that representations in the perirhinal cortex are not stable over time and all representations-including unimodal feature representations-shift between sessions, which could explain these results yet not entail the existence of abstracted object representations.

We thank the reviewer for this suggestion and have conducted the two additional analyses. Specifically, we split the congruent and incongruent conditions and also investigated correlations between unimodal representations on Day 4 with crossmodal object representations on Day 4. There was no significant interaction between modality and congruency in any ROI across or within learning days. One possible explanation for these findings is that both congruent and incongruent crossmodal objects are represented differently from their underlying unimodal features, and all of these representations can transform with experience.

However, the new analyses also revealed that perirhinal cortex was the only region without a modality-specific bias after crossmodal learning (e.g., Day 4 Unimodal Feature runs x Day 4 Crossmodal Object runs; now shown in Supplemental Figure S5). Overall, these results are consistent with the notion of a crossmodal integrative code in perirhinal cortex that has changed with experience and is different from the component unimodal features. Nevertheless, we explore alternative interpretations for how the crossmodal code emerges with experience in the discussion.

“To examine whether these results differed by congruency (i.e., whether any modality-specific biases differed as a function of whether the object was congruent or incongruent), we conducted exploratory linear mixed models for each of the five a priori ROIs across learning days. More specifically, we correlated: 1) the voxel-wise activity for Unimodal Feature Runs before crossmodal learning to the voxel-wise activity for Crossmodal Object Runs before crossmodal learning (Day 2 vs. Day 2), 2) the voxel-wise activity for Unimodal Feature Runs before crossmodal learning to the voxel-wise activity for Crossmodal Object Runs after crossmodal learning (Day 2 vs Day 4), and 3) the voxel-wise activity for Unimodal Feature Runs after crossmodal learning to the voxel-wise activity for Crossmodal Object Runs after crossmodal learning (Day 4 vs Day 4). For each of the three analyses described, we then conducted separate linear mixed models which included modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object) and congruency (congruent vs. incongruent)….There was no significant relationship between modality and congruency in any ROI between Day 2 and Day 2 (F1,346-368 between 0.00 and 1.06, p between 0.30 and 0.99), between Day 2 and Day 4 (F1,346-368 between 0.021 and 0.91, p between 0.34 and 0.89), or between Day 4 and Day 4 (F1,346-368 between 0.01 and 3.05, p between 0.082 and 0.93). However, exploratory analyses revealed that perirhinal cortex was the only region without a modality-specific bias and where the unimodal feature runs were not significantly correlated to the crossmodal object runs after crossmodal learning (Supplemental Figure S5).” – pg. 14

“Taken together, the overall pattern of results suggests that representations of the crossmodal objects in perirhinal cortex were heavily influenced by their consistent visual features before crossmodal learning. However, the crossmodal object representations were no longer influenced by the component visual features after crossmodal learning (Figure 5, Supplemental Figure S5). Additional exploratory analyses did not find evidence of experience-dependent changes in the hippocampus or inferior parietal lobes (Supplemental Figure S4c-e).” – pg. 14

“The voxel-wise matrix for Unimodal Feature runs on Day 4 were correlated to the voxel-wise matrix for Crossmodal Object runs on Day 4 (see Figure 5 in the main text for an example). We compared the average pattern similarity (z-transformed Pearson correlation) between shape (blue) and sound (orange) features specifically after crossmodal learning. Consistent with Figure 5b, perirhinal cortex was the only region without a modality-specific bias. Furthermore, perirhinal cortex was the only region where the representations of both the visual and sound features were not significantly correlated to the crossmodal objects. By contrast, every other region maintained a modality-specific bias for either the visual or sound features. These results suggest that perirhinal cortex representations were transformed with experience, such that the initial visual shape representations (Figure 5a) were no longer grounded in a single modality after crossmodal learning. Furthermore, these results suggest that crossmodal learning formed an integrative code different from the unimodal features in perirhinal cortex, as the visual and sound features were not significantly correlated with the crossmodal objects. * p < 0.05, ** p < 0.01, *** p < 0.001. Horizontal lines within brain regions indicate a significant main effect of modality. Vertical asterisks denote pattern similarity comparisons relative to 0.” – Supplemental Figure S5

“We found that the temporal pole and perirhinal cortex – two anterior temporal lobe structures – came to represent new crossmodal object concepts with learning, such that the acquired crossmodal object representations were different from the representation of the constituent unimodal features (Figure 5, 6). Intriguingly, the perirhinal cortex was by default biased towards visual shape, but that this initial visual bias was attenuated with experience (Figure 3c, 5, Supplemental Figure S5). Within the perirhinal cortex, the acquired crossmodal object concepts (measured after crossmodal learning) became less similar to their original component unimodal features (measured at baseline before crossmodal learning); Figure 5, 6, Supplemental Figure S5. This is consistent with the idea that object representations in perirhinal cortex integrate the component sensory features into a whole that is different from the sum of the component parts, which might be a mechanism by which object concepts obtain their abstraction…. As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation.” – pg. 18

In sum, the authors have collected a fantastic dataset that has the potential to answer questions about the formation of multimodal object representations in the brain. A more precise delineation of different theoretical accounts and additional analyses are needed to provide convincing support for the theory that “explicit integrative” multimodal object representations are formed during learning.

We thank the reviewer for the positive comments and helpful feedback. We hope that our changes to our wording and clarifications to our methodology now more clearly supports the central goal of our study: to find evidence of crossmodal integrative coding different from the original unimodal feature parts in anterior temporal lobe structures. We furthermore agree that future research is needed to delineate the structure of the integrative code that emerges with experience in the anterior temporal lobes.

Reviewer #3 (Public Review):

This paper uses behavior and functional brain imaging to understand how neural and cognitive representations of visual and auditory stimuli change as participants learn associations among them. Prior work suggests that areas in the anterior temporal (ATL) and perirhinal cortex play an important role in learning/representing cross-modal associations, but the hypothesis has not been directly tested by evaluating behavior and functional imaging before and after learning cross- modal associations. The results show that such learning changes both the perceived similarities amongst stimuli and the neural responses generated within ATL and perirhinal regions, providing novel support for the view that cross-modal learning leads to a representational change in these regions.

This work has several strengths. It tackles an important question for current theories of object representation in the mind and brain in a novel and quite direct fashion, by studying how these representations change with cross-modal learning. As the authors note, little work has directly assessed representational change in ATL following such learning, despite the widespread view that ATL is critical for such representation. Indeed, such direct assessment poses several methodological challenges, which the authors have met with an ingenious experimental design. The experiment allows the authors to maintain tight control over both the familiarity and the perceived similarities amongst the shapes and sounds that comprise their stimuli so that the observed changes across sessions must reflect learned cross-modal associations among these. I especially appreciated the creation of physical objects that participants can explore and the approach to learning in which shapes and sounds are initially experienced independently and later in an associated fashion. In using multi-echo MRI to resolve signals in ventral ATL, the authors have minimized a key challenge facing much work in this area (namely the poor SNR yielded by standard acquisition sequences in ventral ATL). The use of both univariate and multivariate techniques was well-motivated and helpful in testing the central questions. The manuscript is, for the most part, clearly written, and nicely connects the current work to important questions in two literatures, specifically (1) the hypothesized role of the perirhinal cortex in representing/learning complex conjunctions of features and (2) the tension between purely embodied approaches to semantic representation vs the view that ATL regions encode important amodal/crossmodal structure.

There are some places in the manuscript that would benefit from further explanation and methodological detail. I also had some questions about the results themselves and what they signify about the roles of ATL and the perirhinal cortex in object representation.

We thank the reviewer for their positive feedback and address the comments in the below point-by-point responses.

(A) I found the terms "features" and "objects" to be confusing as used throughout the manuscript, and sometimes inconsistent. I think by "features" the authors mean the shape and sound stimuli in their experiment. I think by "object" the authors usually mean the conjunction of a shape with a sound---for instance, when a shape and sound are simultaneously experienced in the scanner, or when the participant presses a button on the shape and hears the sound. The confusion comes partly because shapes are often described as being composed of features, not features in and of themselves. (The same is sometimes true of sounds). So when reading "features" I kept thinking the paper referred to the elements that went together to comprise a shape. It also comes from ambiguous use of the word object, which might refer to (a) the 3D- printed item that people play with, which is an object, or (b) a visually-presented shape (for instance, the localizer involved comparing an "object" to a "phase-scrambled" stimulus---here I assume "object" refers to an intact visual stimulus and not the joint presentation of visual and auditory items). I think the design, stimuli, and results would be easier for a naive reader to follow if the authors used the terms "unimodal representation" to refer to cases where only visual or auditory input is presented, and "cross-modal" or "conjoint" representation when both are present.

We thank the reviewer for this suggestion and agree. We have replaced the terms “features” and “objects” with “unimodal” and “crossmodal” in the title, text, and figures throughout the manuscript for consistency (i.e., “crossmodal binding problem”). To simplify the terminology, we have also removed the localizer results.

(B) There are a few places where I wasn't sure what exactly was done, and where the methods lacked sufficient detail for another scientist to replicate what was done. Specifically:

(1) The behavioral study assessing perceptual similarity between visual and auditory stimuli was unclear. The procedure, stimuli, number of trials, etc, should be explained in sufficient detail in methods to allow replication. The results of the study should also minimally be reported in the supplementary information. Without an understanding of how these studies were carried out, it was very difficult to understand the observed pattern of behavioral change. For instance, I initially thought separate behavioral blocks were carried out for visual versus auditory stimuli, each presented in isolation; however, the effects contrast congruent and incongruent stimuli, which suggests these decisions must have been made for the conjoint presentation of both modalities. I'm still not sure how this worked. Additionally, the manuscript makes a brief mention that similarity judgments were made in the context of "all stimuli," but I didn't understand what that meant. Similarity ratings are hugely sensitive to the contrast set with which items appear, so clarity on these points is pretty important. A strength of the design is the contention that shape and sound stimuli were psychophysically matched, so it is important to show the reader how this was done and what the results were.

We agree and apologize for the lack of sufficient detail in the original manuscript. We now include much more detail about the similarity rating task. The methodology and results of the behavioral rating experiments are now shown in Supplemental Figure S1. In Figure S1a, the similarity ratings are visualized on a multidimensional scaling plot. The triangular geometry for shape (blue) and sound (red) indicate that the subjective similarity was equated within each unimodal feature across individual participants. Quantitatively, there was no difference in similarity between the congruent and incongruent pairings in Figure S1b and Figure S1c prior to crossmodal learning. In addition to providing more information on these methods in the Supplemental Information, we also now provide a more detailed description of the task in the manuscript itself. For convenience, we reproduce these sections below.

“Pairwise Similarity Task. Using the same task as the stimulus validation procedure (Supplemental Figure S1a), participants provided similarity ratings for all combinations of the 3 validated shapes and 3 validated sounds (each of the six features were rated in the context of every other feature in the set, with 4 repeats of the same feature, for a total of 72 trials). More specifically, three stimuli were displayed on each trial, with one at the top and two at the bottom of the screen in the same procedure as we have used previously27. The 3D shapes were visually displayed as a photo, whereas sounds were displayed on screen in a box that could be played over headphones when clicked with the mouse. The participant made an initial judgment by selecting the more similar stimulus on the bottom relative to the stimulus on the top. Afterwards, the participant made a similarity rating between each bottom stimulus with the top stimulus from 0 being no similarity to 5 being identical. This procedure ensured that ratings were made relative to all other stimuli in the set.”– pg. 28

“Pairwise similarity task and results. In the initial stimulus validation experiment, participants provided pairwise ratings for 5 sounds and 3 shapes. The shapes were equated in their subjective similarity that had been selected from a well-characterized perceptually uniform stimulus space27 and the pairwise ratings followed the same procedure as described in ref 27. Based on this initial experiment, we then selected the 3 sounds from the that were most closely equated in their subjective similarity. (a) 3D-printed shapes were displayed as images, whereas sounds were displayed in a box that could be played when clicked by the participant. Ratings were averaged to produce a similarity matrix for each participant, and then averaged to produce a group-level similarity matrix. Shown as triangular representational geometries recovered from multidimensional scaling in the above, shapes (blue) and sounds (orange) were approximately equated in their subjective similarity. These features were then used in the four-day crossmodal learning task. (b) Behavioral results from the four-day crossmodal learning task paired with multi-echo fMRI described in the main text. Before crossmodal learning, there was no difference in similarity between shape and sound features associated with congruent objects compared to incongruent objects – indicating that similarity was controlled at the unimodal feature-level. After crossmodal learning, we observed a robust shift in the magnitude of similarity. The shape and sound features associated with congruent objects were now significantly more similar than the same shape and sound features associated with incongruent objects (p < 0.001), evidence that crossmodal learning changed how participants experienced the unimodal features (observed in 17/18 participants). (c) We replicated this learning-related shift in pattern similarity with a larger sample size (n = 44; observed in 38/44 participants). *** denotes p < 0.001. Horizontal lines denote the comparison of congruent vs. incongruent conditions. – Supplemental Figure S1

(2) The experiences through which participants learned/experienced the shapes and sounds were unclear. The methods mention that they had one minute to explore/palpate each shape and that these experiences were interleaved with other tasks, but it is not clear what the other tasks were, how many such exploration experiences occurred, or how long the total learning time was. The manuscript also mentions that participants learn the shape-sound associations with 100% accuracy but it isn't clear how that was assessed. These details are important partly b/c it seems like very minimal experience to change neural representations in the cortex.

We apologize for the lack of detail and agree with the reviewer’s suggestions – we now include much more information in the methods section. Each behavioral day required about 1 hour of total time to complete, and indeed, participants rapidly learned their associations with minimal experience. For example:

“Behavioral Tasks. On each behavioral day (Day 1 and Day 3; Figure 2), participants completed the following tasks, in this order: Exploration Phase, one Unimodal Feature 1-back run (26 trials), Exploration Phase, one Crossmodal 1-back run (26 trials), Exploration Phase, Pairwise Similarity Task (24 trials), Exploration Phase, Pairwise Similarity Task (24 trials), Exploration Phase, Pairwise Similarity Task (24 trials), and finally, Exploration Phase. To verify learning on Day 3, participants also additionally completed a Learning Verification Task at the end of the session. – pg. 27

“The overall procedure ensured that participants extensively explored the unimodal features on Day 1 and the crossmodal objects on Day 3. The Unimodal Feature and the Crossmodal Object 1-back runs administered on Day 1 and Day 3 served as practice for the neuroimaging sessions on Day 2 and Day 4, during which these 1-back tasks were completed. Each behavioral session required less than 1 hour of total time to complete.” – pg. 27

“Learning Verification Task (Day 3 only). As the final task on Day 3, participants completed a task to ensure that participants successfully formed their crossmodal pairing. All three shapes and sounds were randomly displayed in 6 boxes on a display. Photos of the 3D shapes were shown, and sounds were played by clicking the box with the mouse cursor. The participant was cued with either a shape or sound, and then selected the corresponding paired feature. At the end of Day 3, we found that all participants reached 100% accuracy on this task (10 trials).” – pg. 29

(3) I didn't understand the similarity metric used in the multivariate imaging analyses. The manuscript mentions Z-scored Pearson's r, but I didn't know if this meant (a) many Pearson coefficients were computed and these were then Z-scored, so that 0 indicates a value equal to the mean Pearson correlation and 1 is equal to the standard deviation of the correlations, or (b) whether a Fisher Z transform was applied to each r (so that 0 means r was also around 0). From the interpretation of some results, I think the latter is the approach taken, but in general, it would be helpful to see, in Methods or Supplementary information, exactly how similarity scores were computed, and why that approach was adopted. This is particularly important since it is hard to understand the direction of some key effects.

The reviewer is correct that the Fisher Z transform was applied to each individual r before averaging the correlations. This approach is generally recommended when averaging correlations (see Corey, Dunlap, & Burke, 1998). We are now clearer on this point in the manuscript:

“The z-transformed Pearson’s correlation coefficient was used as the distance metric for all pattern similarity analyses. More specifically, each individual Pearson correlation was Fisher z-transformed and then averaged (see 61).” – pg. 32

(C) From Figure 3D, the temporal pole mask appears to exclude the anterior fusiform cortex (or the ventral surface of the ATL generally). If so, this is a shame, since that appears to be the locus most important to cross-modal integration in the "hub and spokes" model of semantic representation in the brain. The observation in the paper that the perirhinal cortex seems initially biased toward visual structure while more superior ATL is biased toward auditory structure appears generally consistent with the "graded hub" view expressed, for instance, in our group's 2017 review paper (Lambon Ralph et al., Nature Reviews Neuroscience). The balance of visual- versus auditory-sensitivity in that work appears balanced in the anterior fusiform, just a little lateral to the anterior perirhinal cortex. It would be helpful to know if the same pattern is observed for this area specifically in the current dataset.

We thank the reviewer for this suggestion. After close inspection of Lambon Ralph et al. (2017), we believe that our perirhinal cortex mask appears to be overlapping with the ventral ATL/anterior fusiform region that the reviewer mentions. See Author response image 1 for a visual comparison:

Author response image 1.

The top four figures are sampled from Lambon Ralph et al (2017), whereas the bottom two figures visualize our perirhinal cortex mask (white) and temporal pole mask (dark green) relative to the fusiform cortex. The ROIs visualized were defined from the Harvard-Oxford atlas.

We now mention this area of overlap in our manuscript and link it to the hub and spokes model:

“Notably, our perirhinal cortex mask overlaps with a key region of the ventral anterior temporal lobe thought to be the central locus of crossmodal integration in the “hub and spokes” model of semantic representations.9,50 – pg. 20

(D) While most effects seem robust from the information presented, I'm not so sure about the analysis of the perirhinal cortex shown in Figure 5. This compares (I think) the neural similarity evoked by a unimodal stimulus ("feature") to that evoked by the same stimulus when paired with its congruent stimulus in the other modality ("object"). These similarities show an interaction with modality prior to cross-modal association, but no interaction afterward, leading the authors to suggest that the perirhinal cortex has become less biased toward visual structure following learning. But the plots in Figures 4a and b are shown against different scales on the y-axes, obscuring the fact that all of the similarities are smaller in the after-learning comparison. Since the perirhinal interaction was already the smallest effect in the pre-learning analysis, it isn't really surprising that it drops below significance when all the effects diminish in the second comparison. A more rigorous test would assess the reliability of the interaction of comparison (pre- or post-learning) with modality. The possibility that perirhinal representations become less "visual" following cross-modal learning is potentially important so a post hoc contrast of that kind would be helpful.

We apologize for the lack of clarity. We conducted a linear mixed model to assess the interaction between modality and crossmodal learning day (before and after crossmodal learning) in the perirhinal cortex as described by the reviewer. The critical interaction was significant, which is now clarified in the text as well as in the rescaled figure plots.

“To investigate this effect in perirhinal cortex more specifically, we conducted a linear mixed model to directly compare the change in the visual bias of perirhinal representations from before crossmodal learning to after crossmodal learning (green regions in Figure 5a vs. 5b). Specifically, the linear mixed model included learning day (before vs. after crossmodal learning) and modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object). Results revealed a significant interaction between learning day and modality in the perirhinal cortex (F1,775 = 5.56, p = 0.019, η2 = 0.071), meaning that the baseline visual shape bias observed in perirhinal cortex (green region of Figure 5a) was significantly attenuated with experience (green region of Figure 5b). After crossmodal learning, a given shape no longer invoked significant pattern similarity between objects that had the same shape but differed in terms of what they sounded like. Taken together, these results suggest that prior to learning the crossmodal objects, the perirhinal cortex had a default bias toward representing the visual shape information and was not representing sound information of the crossmodal objects. After crossmodal learning, however, the visual shape bias in perirhinal cortex was no longer present. That is, with crossmodal learning, the representations within perirhinal cortex started to look less like the visual features that comprised the crossmodal objects, providing evidence that the perirhinal representations were no longer predominantly grounded in the visual modality.” – pg. 13

We note that not all effects drop in Figure 5b (even in regions with a similar numerical pattern similarity to PRC, like the hippocampus – also see Supplemental Figure S5 for a comparison for patterns only on Day 4), suggesting that the change in visual bias in PRC is not simply due to noise.

“Importantly, the change in pattern similarity in the perirhinal cortex across learning days (Figure 5) is unlikely to be driven by noise, poor alignment of patterns across sessions, or generally reduced responses. Other regions with numerically similar pattern similarity to perirhinal cortex did not change across learning days (e.g., visual features x crossmodal objects in A1 in Figure 5; the exploratory ROI hippocampus with numerically similar pattern similarity to perirhinal cortex also did not change in Supplemental Figure S4c-d).” – pg. 14

(E) Is there a reason the authors did not look at representation and change in the hippocampus? As a rapid-learning, widely-connected feature-binding mechanism, and given the fairly minimal amount of learning experience, it seems like the hippocampus would be a key area of potential import for the cross-modal association. It also looks as though the hippocampus is implicated in the localizer scan (Figure 3c).

We thank the reviewer for this suggestion and now include additional analyses for the hippocampus. We found no evidence of crossmodal integrative coding different from the unimodal features. Rather, the hippocampus seems to represent the convergence of unimodal features, as evidenced by …[can you give some pithy description for what is meant by “convergence” vs “integration”?]. We provide these results in the Supplemental Information and describe them in the main text:

“Analyses for the hippocampus (HPC) and inferior parietal lobe (IPL). (a) In the visual vs. auditory univariate analysis, there was no visual or sound bias in HPC, but there was a bias towards sounds that increased numerically after crossmodal learning in the IPL. (b) Pattern similarity analyses between unimodal features associated with congruent objects and incongruent objects. Similar to Supplemental Figure S3, there was no main effect of congruency in either region. (c) When we looked at the pattern similarity between Unimodal Feature runs on Day 2 to Crossmodal Object runs on Day 2, we found that there was significant pattern similarity when there was a match between the unimodal feature and the crossmodal object (e.g., pattern similarity > 0). This pattern of results held when (d) correlating the Unimodal Feature runs on Day 2 to Crossmodal Object runs on Day 4, and (e) correlating the Unimodal Feature runs on Day 4 to Crossmodal Object runs on Day 4. Finally, (f) there was no significant pattern similarity between Crossmodal Object runs before learning correlated to Crossmodal Object after learning in HPC, but there was significant pattern similarity in IPL (p < 0.001). Taken together, these results suggest that both HPC and IPL are sensitive to visual and sound content, as the (c, d, e) unimodal feature-level representations were correlated to the crossmodal object representations irrespective of learning day. However, there was no difference between congruent and incongruent pairings in any analysis, suggesting that HPC and IPL did not represent crossmodal objects differently from the component unimodal features. For these reasons, HPC and IPL may represent the convergence of unimodal feature representations (i.e., because HPC and IPL were sensitive to both visual and sound features), but our results do not seem to support these regions in forming crossmodal integrative coding distinct from the unimodal features (i.e., because representations in HPC and IPL did not differentiate the congruent and incongruent conditions and did not change with experience). * p < 0.05, ** p < 0.01, *** p < 0.001. Asterisks above or below bars indicate a significant difference from zero. Horizontal lines within brain regions in (a) reflect an interaction between modality and learning day, whereas horizontal lines within brain regions in reflect main effects of (b) learning day, (c-e) modality, or (f) congruency.” – Supplemental Figure S4.

“Notably, our perirhinal cortex mask overlaps with a key region of the ventral anterior temporal lobe thought to be the central locus of crossmodal integration in the “hub and spokes” model of semantic representations.9,50 However, additional work has also linked other brain regions to the convergence of unimodal representations, such as the hippocampus51,52,53 and inferior parietal lobes.54,55 This past work on the hippocampus and inferior parietal lobe does not necessarily address the crossmodal binding problem that was the main focus of our present study, as previous findings often do not differentiate between crossmodal integrative coding and the convergence of unimodal feature representations per se. Furthermore, previous studies in the literature typically do not control for stimulus-based factors such as experience with unimodal features, subjective similarity, or feature identity that may complicate the interpretation of results when determining regions important for crossmodal integration. Indeed, we found evidence consistent with the convergence of unimodal feature-based representations in both the hippocampus and inferior parietal lobes (Supplemental Figure S4), but no evidence of crossmodal integrative coding different from the unimodal features. The hippocampus and inferior parietal lobes were both sensitive to visual and sound features before and after crossmodal learning (see Supplemental Figure S4c-e). Yet the hippocampus and inferior parietal lobes did not differentiate between the congruent and incongruent conditions or change with experience (see Supplemental Figure S4).” – pg. 20

(F) The direction of the neural effects was difficult to track and understand. I think the key observation is that TP and PRh both show changes related to cross-modal congruency - but still it would be helpful if the authors could articulate, perhaps via a schematic illustration, how they think representations in each key area are changing with the cross-modal association. Why does the temporal pole come to activate less for congruent than incongruent stimuli (Figure 3)? And why do TP responses grow less similar to one another for congruent relative to incongruent stimuli after learning (Figure 4)? Why are incongruent stimulus similarities anticorrelated in their perirhinal responses following cross-modal learning (Figure 6)?

We thank the author for identifying this issue, which was also raised by the other reviewers. The reviewer is correct that the key observation is that the TP and PRC both show changes related to crossmodal congruency (given that the unimodal features were equated in the methodological design). However, the structure of the integrative code is less clear, which we now emphasize in the main text. Our findings provide evidence of a crossmodal integrative code that is different from the unimodal features, and future studies are needed to better understand the structure of how such a code might emerge. We now more clearly highlight this distinction throughout the paper:

“By contrast, perirhinal cortex may be involved in pattern separation following crossmodal experience. In our task, participants had to differentiate congruent and incongruent objects constructed from the same three shape and sound features (Figure 2). An efficient way to solve this task would be to form distinct object-level outputs from the overlapping unimodal feature-level inputs such that congruent objects are made to be orthogonal from the representations before learning (i.e., measured as pattern similarity equal to 0 in the perirhinal cortex; Figure 5b, 6, Supplemental Figure S5), whereas non-learned incongruent objects could be made to be dissimilar from the representations before learning (i.e., anticorrelation, measured as patten similarity less than 0 in the perirhinal cortex; Figure 6). Because our paradigm could decouple neural responses to the learned object representations (on Day 4) from the original component unimodal features at baseline (on Day 2), these results could be taken as evidence of pattern separation in the human perirhinal cortex.11,12 However, our pattern of results could also be explained by other types of crossmodal integrative coding. For example, incongruent object representations may be less stable than congruent object representations, such that incongruent objects representation are warped to a greater extent than congruent objects (Figure 6).” – pg. 18

“As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation. Furthermore, these anterior temporal lobe structures may be involved with integrative coding in different ways. For example, the crossmodal object representations measured after learning were found to be related to the component unimodal feature representations measured before learning in the temporal pole but not the perirhinal cortex (Figure 5, 6, Supplemental Figure S5). Moreover, pattern similarity for congruent shape-sound pairs were lower than the pattern similarity for incongruent shape-sound pairs after crossmodal learning in the temporal pole but not the perirhinal cortex (Figure 4b, Supplemental Figure S3a). As one interpretation of this pattern of results, the temporal pole may represent new crossmodal objects by combining previously learned knowledge. 8,9,10,11,13,14,15,33 Specifically, research into conceptual combination has linked the anterior temporal lobes to compound object concepts such as “hummingbird”.34,35,36 For example, participants during our task may have represented the sound-based “humming” concept and visually-based “bird” concept on Day 1, forming the crossmodal “hummingbird” concept on Day 3; Figure 1, 2, which may recruit less activity in temporal pole than an incongruent pairing such as “barking-frog”. For these reasons, the temporal pole may form a crossmodal object code based on pre-existing knowledge, resulting in reduced neural activity (Figure 3d) and pattern similarity towards features associated with learned objects (Figure 4b).” – pg. 18

This work represents a key step in our advancing understanding of object representations in the brain. The experimental design provides a useful template for studying neural change related to the cross-modal association that may prove useful to others in the field. Given the broad variety of open questions and potential alternative analyses, an open dataset from this study would also likely be a considerable contribution to the field.

Author Response:

Reviewer #1:

In this manuscript Hill et al, analyze immune responses to vaccination of adults with the seasonal influenza vaccine. They perform a detailed analysis of the hemagglutinin-specific binding antibody responses against several different strains of influenza, and antigen-specific CD4+ T cells/T follicular cells, and cytokines in the plasma. Their analysis reveals that: (i) tetramer positive, HA-specific T follicular cells induced 7 days post vaccination correlate with the binding Ab response measured 42 days later; (ii) the HA-specific T fh have a diverse TCR repertoire; (iii) Impaired differentiation of HA-specific T fh in the elderly; and (iv) identification of an "inflammatory" gene signature within T fh in the elderly, which is associated with the impaired development of HA-specific Tfh.

The paper addresses a topic of considerable interest in the fields of human immunology and vaccinology. In general the experiments appear well performed, and support the conclusions. However, the following points should be addressed to enhance the clarity of the paper, and add support to the key conclusions drawn.

We thank the reviewer for their supportive evaluation of the manuscript, and have provided the details of how we have addressed each the points raised below.

1) Abstract: "(cTfh) cells are the best predictor of high titre antibody responses.." Since the authors have not done any blind prediction using machine learning tools with independent cohort, the sentence should be rephrased thus: "cTfh) cells are were associated with high titre antibody responses."

We agree that this phrasing better reflects the presented data. The sentence in the abstract (page 2) now reads “we show that formation of circulating T follicular helper (cTfh) cells was associated with high titre antibody responses.”

2) Figure 1A: Please indicate the age range of the subjects.

Figure 1 has been updated to include the age range of the subjects.

3) Almost all the data in the paper shows binding Ab titers. Yet, typically HAI titers of MN titers are used to assess Ab responses to influenza. Fig 1C shows HAI titers against the H1N1 Cal 09 strain. Can the authors show HAI titers for Cal 09 and the other A and B strains contained in the 2 vaccine cohorts? Do such HAI titers correlate with the tetramer positive cells, similar to the correlations show in Fig 2e.

In this manuscript we have deliberately focussed on the immune response to the H1N1 Cal09 strain, as it is the only influenza strain in the vaccine common to both cohorts. The HAI titre for this strain is now shown as supplementary figure 4. In addition, the class II tetramers were specifically selected to recognise unique epitopes in the Cal 09 strain (J. Yang, {..} W. W. Kwok, CD4+ T cells recognize unique and conserved 2009 H1N1 influenza hemagglutinin epitopes after natural infection and vaccination. Int Immunol 25, 447-457, 2013) because of this we do not think it is appropriate to correlate HAI titres for the non-Cal 09 strains with tetramer positive cells. We agree that showing the correlation of cTfh and other immune parameters with the HAI titres for Cal 09 is important and have included this as supplementary figure 7. The new data and text are presented below:

Figure 1-figure supplement 4: HAI responses before and after vaccination A) Log2 HAI titres at baseline (d0), d7 and d42 for cohort 1 (n=16) and B) cohort 2 (n = 21). C) Correlation between HAI and A.Cali09 IgG as measured by Luminex assay for cohort 1 and 2 combined. p-values determined using paired Wilcoxon signed rank-test, and Pearson’s correlation.

Text changes. Page 4. “The increase in anti-HA antibody titre was coupled with an increase in hemagglutination inhibitory antibodies to A.Cali09, the one influenza A strain contained in the TIVs that was shared across the two cohorts and showed a positive correlation with the A.Cali09 IgG titres measured by Luminex assay (Fig. 1C, Figure 1-figure supplement 4).”

Figure 2-figure supplement 1: Correlations between HAI assay titres and selected immune parameters. Correlation between vaccine-induced A.Cali09 HAI titres at d42 with selected immune parameters in both Cohort 1 and Cohort 2 (n=37). Dot color corresponds to the cohort (black = Cohort 1, grey = Cohort 2). Coefficient (Rho) and p-value determined using Spearman’s correlation, and line represents linear regression fit.

Results text Changes: Page 5. “Similar trends were seen when these immune parameters were correlated to HAI titres against A/Cali09 (Fig Figure 2-figure supplement 1).”

4) Fig 2d to i: what % of all bulk activated Tfh at day 7 are tetramer positive? The tetramer positive T cells constitute roughly 0.094% of all CD4 T cells (Fig 2d), of which 1/3rd are CXCR5+, PD1+ (i.e. ~0.03% of CD4 T cells). What fraction of all activated Tfh is this subset of tetramer positive cells? Presumably, there will also be Tfh generated against other viral proteins in the vaccine, and these will constitute a significant fraction of all activated Tfh.

This is an important point, as the tetramers only recognise one peptide epitope of the Cal.09 HA protein, so there will be many other influenza reactive CD4+ T cells that are responding to other Cal 09 epitopes as well as other proteins in the vaccine. The analysis suggested by the reviewer shows that the frequency of Tet+ cells amongst bulk cTfh cells ranges from 0.14%-1.52% in cohort 1, and from 0.022-2.7% in cohort 2. These data have been included as Figure Figure 1-figure supplement 6C, D in the revised manuscript. In addition, Tet+ cells as a percentage of bulk cTfh cells were reduced in older people compared to younger adults. This data has been included in Figure 5-figure supplement 1C in the revised manuscript.

Figure 1-figure supplement 6: Percentage of cTfh cells that are Tet+ and CXCR3 and CCR6 expression on HA-specific CD4+ T cells. A) Representative flow cytometry gating strategy for CXCR5+PD-1+ cTfh cells on CD4+CD45RA- T cells, and the proportion of HA-specific Tet+ cells within the CXCR5+PD-1+ cTfh cell gate. B) Percentage Tet+ cells within the CXCR5+PD-1+ cTfh cell population. Within-cohort age group differences were determined using the Mann-Whitney U test.

Results text, page 4: These antigen-specific T cells had upregulated ICOS after immunisation, indicating that they have been activated by vaccination (Fig. 1F, G). In addition, a median of one third of HA-specific T cells upregulated the Tfh markers CXCR5 and PD1 on d7 after immunisation (Fig. 1H, I). The tetramer binding cells represented between 0.022-2.7% of the total CXCR5+PD-1+ bulk population (Fig Figure 1-figure supplement 6A, B).

Figure 5-figure supplement 1C: Age-related differences in cytokines and HA-specific CD4+ T cell parameters. C) Percentage Tet+ cells within the CXCR5+PD-1+ cTfh cell population. Within-cohort age group differences were determined using the Mann-Whitney U test.

Results text, page 8: Across both cohorts, the only CD4+ T cell parameters consistently reduced in older individuals at d7 were the frequency of polyclonal cTfh cells and HA-specific Tet+ cTfh cells, with the strongest effect within the antigen-specific cTfh cell compartment (Fig. 5H-J, Figure 5-figure supplement 1C).

Reviewer #2:

Hill and colleagues present a comprehensive dataset describing the recall and expansion of HA-specific cTFH cells following influenza immunisation in two cohorts. Using class II tetramers, IgG titres against a large panel of HA antigens, and quantification of plasma cytokines, they find that activated and HA-specific cTFH cells were a strong predictor of the IgG response against the vaccine after 6 weeks. Using RNAseq and TCR clonotype analysis, they find that, in 10/15 individuals, the HA-specific cTFH response at day 7 post-vaccination is recalled from the available CD4 T cell memory pool present prior to vaccination. Post-vaccination HA-specific cTFH cells exhibited a transcriptional profile consistent with lymph node-derived GC TFH, as well as evidence of downregulation of IL-2 signaling pathways relative to pre-vaccine CD4 memory cells.

The authors then apply these findings to a comparison of vaccine immunogenicity between younger (18-36) and older (>65) adults. As expected, they found lower levels of vaccine-specific IgG responses among the older cohort. Analysis of HA-specific T cell responses indicated that tet+ cTFH fail to properly develop in the older cohort following vaccination. Further analysis suggests that development of HA-specific cTFH in older individuals is not caused by a lack of TCR diversity, but is associated with higher expression of inflammation-associated transcripts in tet+ cTFH.

Overall this is an impressive study that provides clarity around the recall of HA-specific CD4 T cell memory, and the burst of HA-specific cTFH cells observed 7 days post-vaccination. The association between defective cTFH recall and lower IgG titres post-vaccination in older individuals provides new targets for improving influenza vaccine efficacy in this age group. However, as currently presented, the model of impaired cTFH differentiation in the older cohort and the link to inflammation is somewhat unclear. There are several issues that could be clarified to improve the manuscript in its current form:

We thank the reviewer for their supportive and comprehensive summary of our work. We agree that the link between impaired inflammation and cTfh differentiation is correlative, we have added new data to address this, including mechanistic data to support chronic IL-2 signalling as antagonistic to cTfh development, as well as providing new analyses to address the other points raised.

1) It is somewhat unclear the extent to which the reduction in HA-specific cTFH in the older cohort is also related to an overall reduction in T cell expansion - cohort 1 shows a significant reduction in total tet+ CD4 T cells post-vaccination as well as in the cTFH compartment, and while this difference may not reach statistical significance, a similar trend is shown for cohort 2.

We agree that a possible interpretation is a global failure in T cell expansion in the older individuals. To determine whether there is a relationship between the degree of Tet+ CD4+ T cell expansion and cTfh cell differentiation with age, we performed correlation analyses. There is no correlation between the expansion of Tet+ cells and the frequency of cTfh cells formed seven days after immunisation in either age group. This suggests that the impaired cTfh cell differentiation in older persons is most likely caused by factors other than the capacity of CD4+ T cells to expand after vaccination. These data have been added as Figure 5-figure supplement 1D, and included in the results text on page 8.

Figure 5-figure supplement 1D: Age-related differences in cytokines and HA-specific CD4+ T cell parameters. D) Correlation between Tet+ cells (d7-d0, % of CD4+) and cTfh (d7-d0, % of TET+) in both cohorts for each age-group (18- 36 y.o n=37, 65+ y.o. n= 39). Dot color corresponds to the cohort (black = Cohort 1, grey = Cohort 2). Coefficient (Rho) and p-value determined using Spearman’s correlation, and line represents linear regression fit.

Text changes, Page 8: There was no consistent difference in the total d7 Tet+ HA-specific T cell population with age for both cohorts (Fig. 5H) and we observed no age-related correlation between the ability of an individual to differentiate Tet+ cells into a cTfh cell and the overall expansion of Tet+ HA-specific T cell population (Figure 5-figure supplement 1D). Thus, our data suggests that the poor vaccine antibody responses in older individuals is impacted by impaired cTfh cell differentiation (Fig. 5J) rather than size of the vaccine-specific CD4+ T cell pool.

2) Transcriptomic analysis indicates that HA-specific cTFH in the older cohort show impaired downregulation of inflammation, TNF and IL-2-related signaling pathways. The authors therefore conclude that excess inflammation can limit the response to vaccination. In its current presentation, the data does not necessarily support this conclusion. While it is clear that downregulation of TNF and IL-2 signalling pathways occur during cTFH/TFH differentiation, there is no evidence presented to support the idea that (a) vaccination results in increased pro-inflammatory cytokine production in lymphoid organs in older individuals or that (b) these pro-inflammatory cytokines actively promote CXCR5-, rather than cTFH, differentiation of existing memory T cells.

We agree with the reviewer that the data presented in figure 7 are correlative, rather than causative. Unfortunately, we do not have access to secondary lymphoid tissues from younger and older people after vaccination to test point (a) above. In order to test the hypothesis that increased inflammatory cytokine production in lymphoid organs limits Tfh cell differentiation we have used Il2cre/+; Rosa26stop-flox-Il2/+ transgenic mice. In this mouse model, IL-2-dependent cre- recombinase activity facilitates the expression of low levels of IL-2 in cells that have previously expressed IL-2. This creates a scenario in which cells that physiologically express IL-2 cannot turn its expression off therefore increasing expression IL-2 after antigenic stimulation (mice reported in Whyte et al., bioRxiv, 2020, doi: https://doi.org/10.1101/2020.12.18.423431).

Twelve days after influenza A infection, Il2cre/+; Rosa26stop-flox-Il2/+ transgenic mice have fewer Tfh cells in the draining mediastinal lymph node and in the spleen (Fig. 8A-C), this is accompanied by a reduction in the magnitude of the GC B cell response (Fig. 8D-E). These data provide a proof of concept that sustained IL-2 production limit the formation of Tfh cells, consistent with the negative correlation of an IL-2 signalling gene signature and cTfh cell formation in humans (Figure 7). These new data support the conclusion that excess IL-2 signalling can limit the Tfh cell response. These data are presented in Figure 8, and are discussed on page 12 in the results, and pages 12-13 in the discussion.

Figure 8: Increased IL-2 production impairs Tfh cell formation and the germinal centre response. Assessment of the Tfh cell and germinal centre response in Il2cre/+; Rosa26stop-flox-Il2/+ transgenic mice that do not switch off IL-2 production, and Il2cre/+; Rosa26+/+ control mice 12 days after influenza A infection. Flow cytometric contour plots (A) and quantification of the percentage of CXCR5highPD-1highFoxp3-CD4+ Tfh cells in the mediastinal lymph node (B) and spleen (C). Flow cytometric contour plots (D) and quantification of the percentage of Bcl6+Ki67+B220+ germinal centre B cells in the mediastinal lymph node (E) and spleen (F). The height of the bars indicates the median, each symbol represents one mouse, data are pooled from two independent experiments. P-values calculated between genotype-groups by Mann Whitney U test.

Results text, page 12: Sustained IL-2 production inhibits Tfh cell frequency and the germinal centre response. To test the hypothesis that cytokine signalling needs to be curtailed to facilitate Tfh cell differentiation turned to a genetically modified mouse model in which cells that have initiated IL-2 production cannot switch it off, Il2cre/+; Rosa26stop-flox-Il2/+ mice (37). Twelve days after influenza infection Il2cre/+; Rosa26stop-flox-Il2/+ mice have fewer Tfh cells in the draining lymph node and spleen (Fig. 8A-C), which is associated with a reduced frequency of germinal center B cells (Fig. 8D-F). This provides a proof of concept that proinflammatory cytokine production needs to be limited to enable full Tfh cell differentiation in secondary lymphoid organs.

Discussion text, pages 12, 13: These enhanced inflammatory signatures associated with poor antibody titre in an independent cohort of influenza vaccinees. The dampening of Tfh cell formation by enhanced cytokine production was confirmed by the use of genetically modified mice where IL-2 production is restricted to the appropriate anatomical and cellular compartments, but once initiated cannot be inactivated. Together, this suggests that formation of antigen-specific Tfh cells is essential for high titre antibody responses, and that excessive inflammatory factors can contribute to poor cTfh cell responses.

Author Responses

Reviewer #1 (Public Review):

This study uses a nice longitudinal dataset and performs relatively thorough methodological comparisons. I also appreciate the systematic literature review presented in the introduction. The discussion of confound control is interesting and it is great that a leave-one-site-out test was included. However, the prediction accuracy drops in these important leave-one-site-out analyses, which should be assessed and discussed further.

Furthermore, I think there is a missed opportunity to test longitudinal prediction using only pre-onset individuals to gain clearer causal insights. Please find specific comments below, approximately in order of importance.

We thank the reviewers for their positive remarks and for providing important suggestions to improve the analysis. Please see our detailed comments below.

1) The leave-one-site-out results fail to achieve significant prediction accuracy for any of the phenotypes. This reveals a lack of cross-site generalizability of all results in this work. The authors discuss that this variance could be caused by distributed sample sizes across sites resulting in uneven folds or site-specific variance. It should be possible to test these hypotheses by looking at the relative performance across CV folds. The site-specific variance hypothesis may be likely because for the other results confounds are addressed using oversampling (i.e., sampling with replacement) which creates a large sample with lower variance than a random sample of the same size. This is an important null finding that may have important implications, so I do not think that it is cause for rejection. However, it is a key element of this paper and I think it should be assessed further and discussed more widely in the abstract and conclusion.

We thank the reviewer for raising this point and providing specific suggestions. As mentioned by the reviewer, the leave-one-site-out results showed high-variance across sites, that is, across cross validation (CV) folds. Therefore, as suggested by the reviewer, we further investigated the source of this variance by observing how the model accuracies correlates with each site and its sample sizes, ratio of AAM-to-controls, and the sex distribution in each site. We ranked the sites from low to high accuracy and observed different performance metrics such as sensitivity and specificity:

As shown, the models performed close-to-chance for sites ‘Dublin’, ‘Paris’ and ‘Berlin’ (<60% mean balanced accuracy) in the leave-one-site-out experiment, across all time-points and metrics. Notably, the order of the performance at each site does not correspond to the sample sizes (please refer to the ‘counts’ column in the above figure). It also does not correspond to the ratio of AAM-to-controls, or to the sex distribution.

To further investigate this, we performed another additional leave-one-site-out experiment with all 8 sites. Here, we repeated the ML (Machine Learning) exploration by using the entire data, including the data from the Nottingham site that was kept aside as the holdout. Since there are 8 sites now, we used a 8-fold cross validation and observed how the model accuracy varied across each site:

The results were comparable to the original leave-one-site-out experiment. Along with ‘Dublin’ and Berlin’, the models additionally performed poorly on the ‘Nottingham’ site. Results on ‘London’ and ‘Paris’ also fell below 60% mean balanced accuracy.

Finally, we compared the above two results to the main experiment from the paper where the test samples were randomly sampled across all sites. The performance on test subjects from each site was compared:

As seen, the models struggled with subjects from ‘Dublin’ followed by ‘Nottingham’ ‘London’ and ‘Berlin’ respectively, and performed well on subjects from ‘Dresden’, ‘Mannheim’, ‘Hamburg’ and ‘Paris’.

Across all the three results discussed above, the models consistently struggle to generalize to subjects particularly from ‘Dublin’ and ‘Nottingham’. As already pointed out by the reviewer, the variance in the main experiment in the manuscript is lower because of the random sampling of the test set across all sites. Since these results have important implications, we have included them in the manuscript and also provided these figures in the Appendix.

2) The authors state that "83.3% of subjects reported having no or just one binge drinking experience until age 14". To gain clearer insights into the causality, I recommend repeating the MRIage14 → AAMage22 prediction using only these 83% of subjects.

We thank the reviewer for this valuable comment. As suggested by the reviewer, we now repeated the MRIage14 → AAMage22 analysis by including (a) only the subjects who had no binge drinking experiences (n=477) by age 14 and (b) subjects who had one or less binge drinking experiences (n=565). The results are shown below. The balanced accuracy on the holdout set were 72.9 +/- 2% and 71.1 +/- 2.3% respectively, which is comparable to the main result of 73.1 +/- 2%.

These results provide further evidence that certain form of cerebral predisposition might be preceding the observed alcohol misuse behavior in the IMAGEN dataset. We discuss these results now in the Results section and the 2nd paragraph of Discussion.

3) The feature importance results for brain regions are quite inconsistent across time points. As such, the study doesn't really address one of the main challenges with previous work discussed in the introduction: "brain regions reported were not consistent between these studies either and do not tell a coherent story". This would be worth looking into further, for example by looking at other indices of feature importance such as permutation-based measures and/or investigating the stability of feature importance across bootstrapped CV folds.

The feature importance results shown in Figure 9 is intended to be illustrative and show where the most informative structural features are mainly clustered around in the brain, for each time point. We would like to acknowledge that this figure could be a bit confusing. Hence, we have now provided an exhaustive table in the Appendix, consisting of all important features and their respective SHAP scores obtained across the seven repeated runs. In addition, we address the inconsistencies across time points in the 3rd paragraph in the Discussion chapter and contrast our findings with previous studies. These claims can now be verified from the table of features provided in the Appendix.

Addressing the reviewer's suggestions, we would like to point out that SHAP is itself a type of permutation-based measure of feature importance. Since it derives from the theoretically-sound shapley values, is model agnostic, and has been already applied for biomedical applications, we believe that running another permutation-based analysis would not be beneficial. We have also investigated the stability of our feature importance scores by repeating the SHAP estimation with different random permutations. This process is explained in the Methods section Model Interpretation.

Additionally now, the SHAP scores across the seven repetitions are also provided in the Appendix table 6 for verification.

Author Response

We thank the reviewers for their positive feedback and thoughtful suggestions that will improve our manuscript. Here we summarise our plan for immediate action. We will resubmit our manuscript once additional experiments have been performed to clarify all the major and minor concerns of the reviewers and the manuscript has been revised. At that point, we will respond to all reviewer’s points and highlight the changes made in the text.

Reviewer #1 (Public Review):

The authors have tried to correlate changes in the cellular environment by means of altering temperature, the expression of key cellular factors involved in the viral replication cycle, and small molecules known to affect key viral protein-protein interactions with some physical properties of the liquid condensates of viral origin. The ideas and experiments are extremely interesting as they provide a framework to study viral replication and assembly from a thermodynamic point of view in live cells.

The major strengths of this article are the extremely thoughtful and detailed experimental approach; although this data collection and analysis are most likely extremely time-consuming, the techniques used here are so simple that the main goal and idea of the article become elegant. A second major strength is that in other to understand some of the physicochemical properties of the viral liquid inclusion, they used stimuli that have been very well studied, and thus one can really focus on a relatively easy interpretation of most of the data presented here.

There are three major weaknesses in this article. The way it is written, especially at the beginning, is extremely confusing. First, I would suggest authors should check and review extensively for improvements to the use of English. In particular, the abstract and introduction are extremely hard to understand. Second, in the abstract and introduction, the authors use terms such as "hardening", "perturbing the type/strength of interactions", "stabilization", and "material properties", for just citing some terms. It is clear that the authors do know exactly what they are referring to, but the definitions come so late in the text that it all becomes confusing. The second major weakness is that there is a lack of deep discussion of the physical meaning of some of the measured parameters like "C dense vs inclusion", and "nuclear density and supersaturation". There is a need to explain further the physical consequences of all the graphs. Most of them are discussed in a very superficial manner. The third major weakness is a lack of analysis of phase separations. Some of their data suggest phase transition and/or phase separation, thus, a more in-deep analysis is required. For example, could they calculate the change of entropy and enthalpy of some of these processes? Could they find some boundaries for these transitions between the "hard" (whatever that means) and the liquid?

The authors have achieved almost all their goals, with the caveat of the third weakness I mentioned before. Their work presented in this article is of significant interest and can become extremely important if a more detailed analysis of the thermodynamics parameters is assessed and a better description of the physical phenomenon is provided.

We thank reviewer 1 for the comments and, in particular, for being so positive regarding the strengths of our manuscript and for raising concerns that will surely improve the manuscript. At this point, we propose the following actions to address the concerns of Reviewer 1:

1) We will extensively revise the use of English, particularly, in the abstract and introduction, defining key terms as they come along in the text to make the argument clearer.

2) We acknowledge the importance of discussing our data in more detail and we propose the following. We will discuss the graphs and what they mean as exemplified in the paragraph below.

Regarding Figure 3 - As the concentration of vRNPs increases, we observe an increase in supersaturation until 12hpi. This means that contrary to what is observed in a binary mixture, in which the Cdilute is constant (Klosin et al., 2020), the Cdilute in our system increases with concentration. It has been reported that Cdilute increases in a multi-component system with bulk concentration (Riback et al., 2020). Our findings have important implications for how we think about the condensates formed during influenza infection. As the 8 different genomic vRNPs have a similar overall structure, they could, in theory, behave as a binary system between units of vRNPs and Rab11a. However, a change in Cdilute with concentration shows that our system behaves as a multi-component system. This means that the differences in length, RNA sequence and valency that each vRNP have are key for the integrity of condensates.

3) The reviewer calls our attention to the lack of analysis of phase separations. We think that phase separation (or percolation coupled to phase separation) governs the formation of influenza A virus condensates. However, we think we ought to exert caution at this point as the condensates we are working with are very complex and that the physics of our system in cells may not be sufficient to claim phase separation without an in vitro reconstitution system. In fact, IAV inclusions contain cellular membranes, different vRNPs and Rab11a. So far, we can only speculate that the liquid character of IAV inclusions may arise from a network of interacting vRNPs that bridge several cognate vRNP-Rab11 units on flexible membranes, similarly to what happens in phase separated vesicles in neurological synapses. However, the speculative model for our system, although being supported by correlative light and electron microscopy, currently lacks formal experimental validation.

For this reason, we thought of developing the current work as an alternative to explore the importance of the liquid material properties of IAV inclusions. By finding an efficient method to alter the material properties of IAV inclusions, we provide proof of principle that it is possible to impose controlled phase transitions that reduce the dynamics of vRNPs in cells and negatively impact progeny virion production. Despite having discussed these issues in the limitations of the study, we will make our point clearer.

We are currently establishing an in vitro reconstitution system to formally demonstrate, in an independent publication, that IAV inclusions are formed by phase separation. For this future work, we teamed up with Pablo Sartori, a theorical physicist to derive in- depth analysis of the thermodynamics of the viral liquid condensates. Collectively, we think that cells have too many variables to derive meaningful physics parameters (such as entropy and enthalpy) as well as models and need to be complemented by in vitro systems. For example, increasing the concentration inside a cell is not a simple endeavour as it relies on cellular pathways to deliver material to a specific place. At the same time, the 8 vRNPs, as mentioned above, have different size, valency and RNA sequence and can behave very differently in the formation of condensates and maintenance of their material properties. Ideally, they should be analysed individually or in selected combinations. For the future, we will combine data from in vitro reconstitution systems and cells to address this very important point raised by the reviewer.

From the paper on the section Limitations of the study: “Understanding condensate biology in living cells is physiologically relevant but complex because the systems are heterotypic and away from equilibria. This is especially challenging for influenza A liquid inclusions that are formed by 8 different vRNP complexes, which although sharing the same structure, vary in length, valency, and RNA sequence. In addition, liquid inclusions result from an incompletely understood interactome where vRNPs engage in multiple and distinct intersegment interactions bridging cognate vRNP-Rab11 units on flexible membranes (Chou et al., 2013; Gavazzi et al., 2013; Haralampiev et al., 2020; Le Sage et al., 2020; Shafiuddin & Boon, 2019; Sugita, Sagara, Noda, & Kawaoka, 2013). At present, we lack an in vitro reconstitution system to understand the underlying mechanism governing demixing of vRNP-Rab11a-host membranes from the cytosol. This in vitro system would be useful to explore how the different segments independently modulate the material properties of inclusions, explore if condensates are sites of IAV genome assembly, determine thermodynamic values, thresholds accurately, perform rheological measurements for viscosity and elasticity and validate our findings”.

Reviewer #2 (Public Review):

During Influenza virus infection, newly synthesized viral ribonucleoproteins (vRNPs) form cytosolic condensates, postulated as viral genome assembly sites and having liquid properties. vRNP accumulation in liquid viral inclusions requires its association with the cellular protein Rab11a directly via the viral polymerase subunit PB2. Etibor et al. investigate and compare the contributions of entropy, concentration, and valency/strength/type of interactions, on the properties of the vRNP condensates. For this, they subjected infected cells to the following perturbations: temperature variation (4, 37, and 42{degree sign}C), the concentration of viral inclusion drivers (vRNPs and Rab11a), and the number or strength of interactions between vRNPs using nucleozin a well-characterized vRNP sticker. Lowering the temperature (i.e. decreasing the entropic contribution) leads to a mild growth of condensates that does not significantly impact their stability. Altering the concentration of drivers of IAV inclusions impact their size but not their material properties. The most spectacular effect on condensates was observed using nucleozin. The drug dramatically stabilizes vRNP inclusions acting as a condensate hardener. Using a mouse model of influenza infection, the authors provide evidence that the activity of nucleozin is retained in vivo. Finally, using a mass spectrometry approach, they show that the drug affects vRNP solubility in a Rab11a-dependent manner without altering the host proteome profile.

The data are compelling and support the idea that drugs that affect the material properties of viral condensates could constitute a new family of antiviral molecules as already described for the respiratory syncytial virus (Risso Ballester et al. Nature. 2021).

Nevertheless, there are some limitations in the study. Several of them are mentioned in a dedicated paragraph at the end of a discussion. This includes the heterogeneity of the system (vRNP of different sizes, interactions between viral and cellular partners far from being understood), which is far from equilibrium, and the absence of minimal in vitro systems that would be useful to further characterize the thermodynamic and the material properties of the condensates.

We thank reviewer 2 for highlighting specific details that need improving and raising such interesting questions to validate our findings. We will address all the minor comments of Reviewer 2. To address the comments of Reviewer 2, we propose the actions described in blue below each point raised that is written in italics.

1) The concentrations are mostly evaluated using antibodies. This may be correct for Cdilute. However, measurement of Cdense should be viewed with caution as the antibodies may have some difficulty accessing the inner of the condensates (as already shown in other systems), and this access may depend on some condensate properties (which may evolve along the infection). This might induce artifactual trends in some graphs (as seen in panel 2c), which could, in turn, affect the calculation of some thermodynamic parameters.

The concern of using antibodies to calculate Cdense is valid. We will address this concern by validating our results using a fluorescent tagged virus that has mNeon Green fused to the viral polymerase PA (PA-mNeonGreen PR8 virus). Like NP, PA is a component of vRNPs and labels viral inclusions, colocalising with Rab11 when vRNPs are in the cytosol without the need of using antibodies.

This virus would be the best to evaluate inclusion thermodynamics, where it not an attenuated virus (Figure 1A below) with a delayed infection as demonstrated by the reduced levels of viral proteins (Figure 1B below). Consistently, it shows differences in the accumulation of vRNPs in the cytosol and viral inclusions form later in infection. After their emergence, inclusions behave as in the wild-type virus (PR8-WT), fusing and dividing (Figure 1C below) and displaying liquid properties. The differences in concentration may shift or alter thermodynamic parameters such as time of nucleation, nucleation density, inclusion maturation rate, Cdense, Cdilute. This is the reason why we performed the thermodynamics profiling using antibodies upon PR8-WT infection. For validating our results, and taking into account a possible delayed kinetics, and differenced that may occur because of reduced vRNP accumulation in the cytosol, this virus will be useful and therefore we will repeat the thermodynamics using it.

As a side note, vRNPs are composed of viral RNA coated with several molecules of NP and each vRNP also contains 1 copy of the trimeric RNA dependent RNA polymerase formed by PA, PB1 and PB2. It is well documented that in the cytosol the vast majority of PA (and other components of the polymerase) is in the form of vRNPs (Avilov, Moisy, Munier, et al., 2012; Avilov, Moisy, Naffakh, & Cusack, 2012; Bhagwat et al., 2020; Lakdawala et al., 2014), and thus we can use this virus to label vRNPs on condensates to corroborate our studies using antibodies.

Figure 1 – The PA- mNeonGreen virus is attenuated in comparison to the WT virus. A. Cells (A549) were infected or mock-infected with PR8 WT or PA- mNeonGreen (PA-mNG) viruses, at a multiplicity of infection (MOI) of 3, for the indicated times. Viral production was determined by plaque assay and plotted as plaque forming units (PFU) per milliliter (mL) ± standard error of the mean (SEM). Data are a pool from 2 independent experiments. B. The levels of viral PA, NP and M2 proteins and actin in cell lysates at the indicated time points were determined by western blotting. C. Cells (A549) were transfected with a plasmid encoding mCherry-NP and co-infected with PA-mNeonGreen virus for 16h, at an MOI of 10. Cells were imaged under time-lapse conditions starting at 16 hpi. White boxes highlight vRNPs/viral inclusions in the cytoplasm in the individual frames. The dashed white and yellow lines mark the cell nucleus and the cell periphery, respectively. The yellow arrows indicate the fission/fusion events and movement of vRNPs/ viral inclusions. Bar = 10 µm. Bar in insets = 2 µm.

2) Although the authors have demonstrated that vRNP condensates exhibit several key characteristics of liquid condensates (they fuse and divide, they dissolve upon hypotonic shock or upon incubation with 1,6-hexanediol, FRAP experiments are consistent with a liquid nature), their aspect ratio (with a median above 1.4) is much higher than the aspect ratio observed for other cellular or viral liquid compartments. This is intriguing and might be discussed.

IAV inclusions have been shown to interact with microtubules and the endoplasmic reticulum, that confers movement, and also undergo fusion and fission events. We propose that these interactions and movement impose strength and deform inclusions making them less spherical. To validate this assumption, we compared the aspect ratio of viral inclusions in the absence and presence of nocodazole (that abrogates microtubule-based movement). The data in figure 2 shows that in the presence of nocodazole, the aspect ratio decreases from 1.42±0.36 to 1.26 ±0.17, supporting our assumption.

Figure 2 – Treatment with nocodazole reduces the aspect ratio of influenza A virus inclusions. Cells (A549) were infected PR8 WT and treated with nocodazole (10 µg/mL) for 2h time after which the movement of influenza A virus inclusions was captured by live cell imaging. Viral inclusions were segmented, and the aspect ratio measured by imageJ, analysed and plotted in R.

3) Similarly, the fusion event presented at the bottom of figure 3I is dubious. It might as well be an aggregation of condensates without fusion.

We will change this, thank you for the suggestion.

4) The authors could have more systematically performed FRAP/FLAPh experiments on cells expressing fluorescent versions of both NP and Rab11a to investigate the influence of condensate size, time after infection, or global concentrations of Rab11a in the cell (using the total fluorescence of overexpressed GFP-Rab11a as a proxy) on condensate properties.

We will try our best to be able to comply with this suggestion as we think it is important.

Reviewer #3 (Public Review):

This study aims to define the factors that regulate the material properties of the viral inclusion bodies of influenza A virus (IAV). In a cellular model, it shows that the material properties were not affected by lowering the temperature nor by altering the concentration of the factors that drive their formation. Impressively, the study shows that IAV inclusions may be hardened by targeting vRNP interactions via the known pharmacological modulator (also an IAV antiviral), nucleozin, both in vitro and in vivo. The study employs current state-of-the-art methodology in both influenza virology and condensate biology, and the conclusions are well-supported by data and proper data analysis. This study is an important starting point for understanding how to pharmacologically modulate the material properties of IAV viral inclusion bodies.

We thank this reviewer for all the positive comments. We will address the minor issues brought to our attention entirely, including changing the tittle of the manuscript and we will investigate the formation and material properties of IAV inclusions in the presence and absence of nucleozin for the nucleozin escape mutant NP-Y289H.

References

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Avilov, S. V., Moisy, D., Naffakh, N., & Cusack, S. (2012). Influenza A virus progeny vRNP trafficking in live infected cells studied with the virus-encoded fluorescently tagged PB2 protein. Vaccine, 30(51), 7411-7417. doi:10.1016/j.vaccine.2012.09.077

Bhagwat, A. R., Le Sage, V., Nturibi, E., Kulej, K., Jones, J., Guo, M., . . . Lakdawala, S. S. (2020). Quantitative live cell imaging reveals influenza virus manipulation of Rab11A transport through reduced dynein association. Nat Commun, 11(1), 23. doi:10.1038/s41467-019-13838-3

Chou, Y. Y., Heaton, N. S., Gao, Q., Palese, P., Singer, R. H., & Lionnet, T. (2013). Colocalization of different influenza viral RNA segments in the cytoplasm before viral budding as shown by single-molecule sensitivity FISH analysis. PLoS Pathog, 9(5), e1003358. doi:10.1371/journal.ppat.1003358

Gavazzi, C., Yver, M., Isel, C., Smyth, R. P., Rosa-Calatrava, M., Lina, B., . . . Marquet, R. (2013). A functional sequence-specific interaction between influenza A virus genomic RNA segments. Proc Natl Acad Sci U S A, 110(41), 16604-16609. doi:10.1073/pnas.1314419110

Haralampiev, I., Prisner, S., Nitzan, M., Schade, M., Jolmes, F., Schreiber, M., . . . Herrmann, A. (2020). Selective flexible packaging pathways of the segmented genome of influenza A virus. Nat Commun, 11(1), 4355. doi:10.1038/s41467-020-18108-1

Klosin, A., Oltsch, F., Harmon, T., Honigmann, A., Julicher, F., Hyman, A. A., & Zechner, C. (2020). Phase separation provides a mechanism to reduce noise in cells. Science, 367(6476), 464-468. doi:10.1126/science.aav6691

Lakdawala, S. S., Wu, Y., Wawrzusin, P., Kabat, J., Broadbent, A. J., Lamirande, E. W., . . . Subbarao, K. (2014). Influenza a virus assembly intermediates fuse in the cytoplasm. PLoS Pathog, 10(3), e1003971. doi:10.1371/journal.ppat.1003971

Le Sage, V., Kanarek, J. P., Snyder, D. J., Cooper, V. S., Lakdawala, S. S., & Lee, N. (2020). Mapping of Influenza Virus RNA-RNA Interactions Reveals a Flexible Network. Cell Rep, 31(13), 107823. doi:10.1016/j.celrep.2020.107823

Riback, J. A., Zhu, L., Ferrolino, M. C., Tolbert, M., Mitrea, D. M., Sanders, D. W., . . . Brangwynne, C. P. (2020). Composition-dependent thermodynamics of intracellular phase separation. Nature, 581(7807), 209-214. doi:10.1038/s41586-020-2256-2

Shafiuddin, M., & Boon, A. C. M. (2019). RNA Sequence Features Are at the Core of Influenza a Virus Genome Packaging. J Mol Biol. doi:10.1016/j.jmb.2019.03.018

Sugita, Y., Sagara, H., Noda, T., & Kawaoka, Y. (2013). Configuration of viral ribonucleoprotein complexes within the influenza A virion. J Virol, 87(23), 12879- 12884. doi:10.1128/JVI.02096-13

Author Response

Reviewer #1 (Public Review):

The authors have tried to correlate changes in the cellular environment by means of altering temperature, the expression of key cellular factors involved in the viral replication cycle, and small molecules known to affect key viral protein-protein interactions with some physical properties of the liquid condensates of viral origin. The ideas and experiments are extremely interesting as they provide a framework to study viral replication and assembly from a thermodynamic point of view in live cells.

The major strengths of this article are the extremely thoughtful and detailed experimental approach; although this data collection and analysis are most likely extremely time-consuming, the techniques used here are so simple that the main goal and idea of the article become elegant. A second major strength is that in other to understand some of the physicochemical properties of the viral liquid inclusion, they used stimuli that have been very well studied, and thus one can really focus on a relatively easy interpretation of most of the data presented here.

There are three major weaknesses in this article. The way it is written, especially at the beginning, is extremely confusing. First, I would suggest authors should check and review extensively for improvements to the use of English. In particular, the abstract and introduction are extremely hard to understand. Second, in the abstract and introduction, the authors use terms such as "hardening", "perturbing the type/strength of interactions", "stabilization", and "material properties", for just citing some terms. It is clear that the authors do know exactly what they are referring to, but the definitions come so late in the text that it all becomes confusing. The second major weakness is that there is a lack of deep discussion of the physical meaning of some of the measured parameters like "C dense vs inclusion", and "nuclear density and supersaturation". There is a need to explain further the physical consequences of all the graphs. Most of them are discussed in a very superficial manner. The third major weakness is a lack of analysis of phase separations. Some of their data suggest phase transition and/or phase separation, thus, a more in-deep analysis is required. For example, could they calculate the change of entropy and enthalpy of some of these processes? Could they find some boundaries for these transitions between the "hard" (whatever that means) and the liquid?

The authors have achieved almost all their goals, with the caveat of the third weakness I mentioned before. Their work presented in this article is of significant interest and can become extremely important if a more detailed analysis of the thermodynamics parameters is assessed and a better description of the physical phenomenon is provided.

We thank you for the comments and, in particular, for being so positive regarding the strengths of our manuscript and for raising concerns that will surely improve it. We have taken the following actions to address your concerns:

1) Extensive revisions have been made to the use of English, particularly in the abstract and introduction. Key terms are defined as they are introduced in the text to enhance the clarity of the argument. This is a significant revision that is highlighted within the text, but it is too extensive to detail here.

2) In the results section, we improved and extended the discussion of our graphs to the extent possible. However, we found that attempting to explain the graphs' meanings more thoroughly would detract from our manuscript's main focus: identifying thermodynamic changes that could potentially lead to alterations in material properties, specifically aspect ratio, size, and Gibbs free energy. As a result, we introduced the type of information we could obtain from our analyses in the introduction (Lines 112-125) and briefly commented on it in the ‘results’ section (Lines 304-306, sentences below).

From introduction – lines 112-125:

“In addition, other parameters like nucleation density determine how many viral condensates are formed per area of cytosol. Overall, the data will inform us if changing one parameter, e.g. the concentration, drives the system towards larger condensates with the same or more stable properties, or more abundant condensates that are forced to maintain the initial or a different size on account of available nucleation centres (Riback et al., 2020:Snead, 2022 #1152). It will also inform us if liquid viral inclusions behave like a binary or a multi-component system. In a binary mixture, Cdilute is constant (Klosin et al., 2020). However, in multi-component systems, Cdilute increases with bulk concentration (Riback et al., 2020). This type of information could have direct implications about the condensates formed during influenza infection. As the 8 different genomic vRNPs have a similar overall structure, they could, in theory, behave as a binary system between units of vRNPs and Rab11a. However, a change in Cdilute with concentration would mean that the system behaves as a multi-component system. This could raise the hypothesis that the differences in length, RNA sequence and valency that each vRNP has may be relevant for the integrity and behaviour of condensates.”.

From results lines 304-306:

This indicates that the liquid inclusions behave as a multi-component system and allow us to speculate that the differences in length, RNA sequence and valency that each vRNP may be key for the integrity and behaviour of condensates.

3) The reviewer has drawn our attention to the absence of phase separation analysis in our study. We believe that the formation of influenza A virus condensates is governed by phase separation (or percolation coupled to phase separation). However, we must exercise caution at this point because the condensates we are studying are highly complex, and the physics of our cellular system may not be adequate to claim phase separation without being validated by an in vitro reconstitution system. IAV inclusions contain a variety of cellular membranes, different vRNPs, and Rab11a. While we have robust data to propose a model in which the liquid-like properties of IAV inclusions arise from a network of interacting vRNPs that bridge multiple cognate vRNP-Rab11 units on flexible membranes, similar to what occurs in phase-separated vesicles in neurological synapses, our model for this system still lacks formal experimental validation. As a note, the data supporting our model includes: the demonstration of the liquid properties of our liquid inclusions (Alenquer et al. 2019, Nature Communications, 10, 1629); and impairment of recycling endocytic activity during IAV infection Bhagwat et al. 2020, Nat Commun, 11, 23; Kawaguchi et al. 2012, J Virol, 86, 11086-95; Vale-costa et al. 2016, J Cell Sci, 129, 1697-710. This leads to aggregated vesicles seen by correlative light and electron microscopy (Vale-Costa et al., 2016 JCS, 129, 1697-710) and by immunofluorescence and FISH (Amorim et al. 2011,. J Virol 85, 4143-4156; Avilov et al. 2012, Vaccine 30, 7411-7417; Chou et al. 2013, PLoS Pathog 9, e1003358; Eisfeld et al. 2011, J Virol 85, 6117-6126 and Lakdawala et al. 2014, PLoS Pathog 10, e1003971.

To be able to explore the significance of the liquid material properties of IAV inclusions, we used the strategy described in this current work. By developing an effective method to manipulate the material properties of IAV inclusions, we provide evidence that controlled phase transitions can be induced, resulting in decreased vRNP dynamics in cells and a negative impact on progeny virion production. This suggests that the liquid character of liquid inclusions is important for their function in IAV infection. We have improved our explanation addressing this concern in the limitations of our study (as outlined below in the box and in manuscript in lines 857-872).

We are currently establishing an in vitro reconstitution system to formally demonstrate, in an independent publication, that IAV inclusions are formed by phase separation (or percolation coupled to phase separation). For this future work, we teamed up with Pablo Sartori, a theorical physicist to derive in-depth analysis of the thermodynamics of the viral liquid condensates in the in vitro reconstituted system and compare it to results obtained in the cell. This will provide means to establish comparisons. We think that cells have too many variables to derive meaningful physics parameters (such as entropy and enthalpy) and models that need to be complemented by in vitro systems. For example, increasing the concentration inside a cell is not a simple endeavour as it relies on cellular pathways to deliver material to a specific place. At the same time, the 8 vRNPs, as mentioned above, have different size, valency and RNA sequence and can behave very differently in the formation of condensates and maintenance of their material properties. Ideally, they should be analysed individually or in selected combinations. For the future, we will combine data from in vitro reconstitution systems and cells to address this very important point raised by the reviewer.

From the paper on the section ‘Limitations of the study’:

“Understanding condensate biology in living cells is physiological relevant but complex because the systems are heterotypic and away from equilibria. This is especially challenging for influenza A liquid inclusions that are formed by 8 different vRNP complexes, which although sharing the same structure, vary in length, valency, and RNA sequence. In addition, liquid inclusions result from an incompletely understood interactome where vRNPs engage in multiple and distinct intersegment interactions bridging cognate vRNP-Rab11 units on flexible membranes (Chou et al., 2013, Gavazzi et al., 2013, Sugita et al., 2013, Shafiuddin and Boon, 2019, Haralampiev et al., 2020, Le Sage et al., 2020). At present, we lack an in vitro reconstitution system to understand the underlying mechanism governing demixing of vRNP-Rab11a-host membranes from the cytosol. This in vitro system would be useful to explore how the different segments independently modulate the material properties of inclusions, explore if condensates are sites of IAV genome assembly, determine thermodynamic values, thresholds accurately, perform rheological measurements for viscosity and elasticity and validate our findings. The results could be compared to those obtained in cell systems to derive thermodynamic principles happening in a complex system away from equilibrium. Using cells to map how liquid inclusions respond to different perturbations provide the answer of how the system adapts in vivo, but has limitations.

Reviewer #2 (Public Review):

During Influenza virus infection, newly synthesized viral ribonucleoproteins (vRNPs) form cytosolic condensates, postulated as viral genome assembly sites and having liquid properties. vRNP accumulation in liquid viral inclusions requires its association with the cellular protein Rab11a directly via the viral polymerase subunit PB2. Etibor et al. investigate and compare the contributions of entropy, concentration, and valency/strength/type of interactions, on the properties of the vRNP condensates. For this, they subjected infected cells to the following perturbations: temperature variation (4, 37, and 42{degree sign}C), the concentration of viral inclusion drivers (vRNPs and Rab11a), and the number or strength of interactions between vRNPs using nucleozin a well-characterized vRNP sticker. Lowering the temperature (i.e. decreasing the entropic contribution) leads to a mild growth of condensates that does not significantly impact their stability. Altering the concentration of drivers of IAV inclusions impact their size but not their material properties. The most spectacular effect on condensates was observed using nucleozin. The drug dramatically stabilizes vRNP inclusions acting as a condensate hardener. Using a mouse model of influenza infection, the authors provide evidence that the activity of nucleozin is retained in vivo. Finally, using a mass spectrometry approach, they show that the drug affects vRNP solubility in a Rab11a-dependent manner without altering the host proteome profile

The data are compelling and support the idea that drugs that affect the material properties of viral condensates could constitute a new family of antiviral molecules as already described for the respiratory syncytial virus (Risso Ballester et al. Nature. 2021)

Nevertheless, there are some limitations in the study. Several of them are mentioned in a dedicated paragraph at the end of a discussion. This includes the heterogeneity of the system (vRNP of different sizes, interactions between viral and cellular partners far from being understood), which is far from equilibrium, and the absence of minimal in vitro systems that would be useful to further characterize the thermodynamic and the material properties of the condensates.

There are other ones.

We thank reviewer 2 for highlighting specific details that need improving and raising such interesting questions to validate our findings. We have addressed the comments of Reviewer 2, we performed the experiments as described (in blue) below each point raised.

1) The concentrations are mostly evaluated using antibodies. This may be correct for Cdilute. However, measurement of Cdense should be viewed with caution as the antibodies may have some difficulty accessing the inner of the condensates (as already shown in other systems), and this access may depend on some condensate properties (which may evolve along the infection). This might induce artifactual trends in some graphs (as seen in panel 2c), which could, in turn, affect the calculation of some thermodynamic parameters.

The concern of using antibodies to calculate Cdense is valid, and we thought it was very important. We addressed this concern by performing the same analyses using a fluorescent tagged virus that has mNeon Green fused to the viral polymerase PA (PA-mNeonGreen PR8 virus). Like NP, PA is a component of vRNPs and labels viral inclusions, colocalising with Rab11 when vRNPs are in the cytosol. However, per vRNP there is only one molecule of PA, whilst of NP there are 37-96 depending on the size of vRNPs. As predicted, we did observe changes in the Cdilute, Cdense and nucleation density. However, the measurements and values obtained for Gibbs free energy, size, aspect ratio detecting viral inclusions with fluorescently tagged vRNPs or antibody staining followed the same trend and allow us to validate our conclusion that major changes in Gibbs free energy occur solely when there is a change in the valency/strength of interactions but not in temperature or concentration (Figure 1 below). Given the extent of these data, we show here the results but, in the manuscript, we will describe the limitations of using antibodies in our study within the section ‘Limitations of the study’ from lines 881-894. Given the importance of the question regarding the pros and cons of the different systems for analysing thermodynamic parameters, we have decided to systematically assess and explore these differences in detail in a future manuscript.

For more information. This reviewer may be asking why we did not use the PA-fluorescent virus in the first place to evaluate inclusion thermodynamics and avoid problems in accessibility that antibodies may have to get deep into large inclusions. Our answer is that no system is perfect. In the case of the PA-fluorescent virus, the caveats revolve around the fact that the virus is attenuated (Figure 1a below), exhibiting a delayed infection as demonstrated by reduced levels of viral proteins (Figure 1b below). Consistently, it shows differences in the accumulation of vRNPs in the cytosol and viral inclusions form later in infection and the amount of vRNPs in the cytosol does not reach the levels observed in PR8-WT virus. After their emergence, inclusions behave as in the wild-type virus (PR8-WT), fusing and dividing (Figure 1c below) and displaying liquid properties.

As the overarching goal of this manuscript is to evaluate the best strategies to harden liquid IAV inclusions and given that one of the parameters we were testing is concentration, we reasoned that using PR8-WT virus for our analyses would be reasonable.

In conclusions, both systems have caveats that are important to systematically assess, and these differences may shift or alter thermodynamic parameters such as nucleation density, inclusion maturation rate, Cdense, Cdilute in particular by varying the total concentration. As a note, to validate all our results using the PA-mNeonGreen PR8 virus, we considered the delayed kinetics and applied our thermodynamic analyses up to 20 hpi rather than 16 hpi.

However, because of the question raised by this reviewer, on which is the best solution for mitigating errors induced by using antibodies, we re-checked all our data. Not only have we compared the data originated from attenuated fluorescently tagged virus with our data, but also made comparisons with images acquired from Z stacks (as used for concentration and for type/strength of interactions) with those acquired from 2D images. Our analysis revealed that there is a very good match using images acquired with Z-stacks and analysed as Z projections with between antibody staining and vRNP fluorescent virus. Therefore, we re-analysed all our thermodynamic data done with temperature using images acquired from Z stacks and altered entirely Figure 2. We believe that all these comparisons and analyses have greatly improved the manuscript and hence we thank all reviewers for their input.

Figure 1 – The PA-mNeonGreen virus is attenuated in comparison to the WT virus and data obtained is consistent for Gibbs free energy with analyses done with images processed with antibody fluorescent vRNPs. A. Representation of the PA-mNeonGreen virus (PA-mNG; Abbreviations: NCR: non coding region). B. Cells (A549) were transfected with a plasmid encoding mCherry-NP and co-infected with PA-mNeonGreen virus for 16h, at an MOI of 10. Cells were imaged under time-lapse conditions starting at 16 hpi. White boxes highlight vRNPs/viral inclusions in the cytoplasm in the individual frames. The dashed white and yellow lines mark the cell nucleus and the cell periphery, respectively. The yellow arrows indicate the fission/fusion events and movement of vRNPs/ viral inclusions. Bar = 10 µm. Bar in insets = 2 µm. C-D. Cells (A549) were infected or mock-infected with PR8 WT or PA-mNG viruses, at a multiplicity of infection (MOI) of 3, for the indicated times. C. Viral production was determined by plaque assay and plotted as plaque forming units (PFU) per milliliter (mL) ± standard error of the mean (SEM). Data are a pool from 2 independent experiments. D. The levels of viral PA, NP and M2 proteins and actin in cell lysates at the indicated time points were determined by western blotting. (E-G) Biophysical calculations in cells infected with the PA-mNeonGreen virus upon altering temperature (at 10 hpi, evaluating the concentration of vRNPs (over a time course) in conditions expressing native amounts of Rab11a or overexpressing low levels of Rab11a and upon altering the type/strength of vRNP interactions by adding nucleozin at 10 hpi during the indicated time periods. All data: Ccytoplasm/Cnucleus; Cdense, Cdilute, area aspect ratio and Gibbs free energy are represented as boxplots. Above each boxplot, same letters indicate no significant difference between them, while different letters indicate a statistical significance at α = 0.05 using one-way ANOVA, followed by Tukey multiple comparisons of means for parametric analysis, or Kruskal-Wallis Bonferroni treatment for non-parametric analysis.

2) Although the authors have demonstrated that vRNP condensates exhibit several key characteristics of liquid condensates (they fuse and divide, they dissolve upon hypotonic shock or upon incubation with 1,6-hexanediol, FRAP experiments are consistent with a liquid nature), their aspect ratio (with a median above 1.4) is much higher than the aspect ratio observed for other cellular or viral liquid compartments. This is intriguing and might be discussed.

IAV inclusions have been shown to interact with microtubules and the endoplasmic reticulum, that confers movement, and undergo fusion and fission events. We propose that these interactions and movement impose strength and deform inclusions making them less spherical. To validate this assumption, we compared the aspect ratio of viral inclusions in the absence and presence of nocodazole (that abrogates microtubule-based movement). The data in figure 2 shows that in the presence of nocodazole, the aspect ratio decreases from 1.42±0.36 to 1.26 ±0.17, supporting our assumption.

Figure 2 – Treatment with nocodazole reduces the aspect ratio of influenza A virus inclusions. Cells (A549) were infected with PR8 WT for 8 h and treated with nocodazole (10 µg/mL) for 2h, after which the movement of influenza A virus inclusions was captured by live cell imaging. Viral inclusions were segmented, and the aspect ratio measured by imageJ, analysed and plotted in R.

3) Similarly, the fusion event presented at the bottom of figure 3I is dubious. It might as well be an aggregation of condensates without fusion.

We have changed this (check Fig 5A and B in the manuscript), thank you for the suggestion.

4) The authors could have more systematically performed FRAP/FLAPh experiments on cells expressing fluorescent versions of both NP and Rab11a to investigate the influence of condensate size, time after infection, or global concentrations of Rab11a in the cell (using the total fluorescence of overexpressed GFP-Rab11a as a proxy) on condensate properties.

We have included a new figure, figure 5 with the suggested data.

Author Response

Reviewer #2 (Public Review):

1) The main limitation of this study is that the results are primarily descriptive in nature, and thus, do not provide mechanistic insight into how Ryr1 disease mutations lead to the muscle-specific changes observed in the EDL, soleus and EOM proteomes.

An intrinsic feature of the high-throughput proteomic analysis technology is the generation of lists of differentially expressed proteins (DEP) in different muscles from WT and mutated mice. Although the definition of mechanistic insights related to changes of dozens of proteins is very interesting, it is a difficult task to accomplish and goes beyond the goal of the high-throughput proteomic analysis presented here. Nevertheless, the analysis of DEPs may indeed provide arguments to speculate on the pathogenesis of the phenotype linked to recessive RyR1 mutations. In the unrevised manuscript, we pointed out that the fiber type I predominance observed in congenital myopathies linked to recessive Ryr1 mutation are consistent with the high expression level of heat shock proteins in slow twitch muscles. However, as suggested by Reviewer 3, we have removed "vague statements" from the text of the revised manuscript, concerning major insights into pathophysiological mechanisms, since we are aware that the mechanistic information, if any, that we can extract from the data set, cannot go over the intrinsic limitation of the high-throughput proteomic technology.

b) Results comparing fast twitch (EDL) and slow twitch (soleus) muscles from WT mice confirmed several known differences between the two muscle types. Similar analyses between EOM/EDL and EOM/soleus muscles from WT mice were not conducted.

We agree with the point raised by the Reviewer. In the revised manuscript we have changed Figure 2. The new Figure 2 shows the analysis of differentially expressed proteins in EDL, soleus and EOMs from WT mice. We have also added 2 new Tables (new Supplementary Table 2 and 3) and have inserted our findings in the revised Results section (page, 7, lines 157-176, pages 8 and 9).

c) While a reactome pathway analysis for proteins changes observed in EDL is shown in Supplemental Figure 1, the authors do not fully discuss the nature of the proteins and corresponding pathways impacted in the other two muscle groups analyzed.

We have now included in the revised manuscript a new Figure 2 which includes the Reactome pathway analysis comparing EDL with soleus, EDL with EOM and soleus with EOM (panels C, F and I, respectively). We have also inserted into the revised manuscript a brief description of the pathways showing the greatest changes in protein content (page 7 line 156-175, pages 8 and 9). We agree that the data showing changes in protein content between the 3 muscle groups of the WT mice are important also because they validate the results of the proteomic approach. Indeed, the present results confirm that many proteins including MyHCIIb, calsequestrin 1, SERCA1, parvalbumin etc are more abundantly expressed in fast twitch EDL muscles compared to soleus. Similarly, our results confirm that EOMs are enriched in MyHC-EO as well as cardiac isoforms of ECC proteins. This point has been clarified in the revised version of the manuscript (page 8, lines 198-213; page 9 lines 214-228). Nevertheless, we would like to point out that the main focus of our study is to compare the changes of protein content induced by the presence of recessive RyR1 mutations.

Reviewer #3 (Public Review):

a) it would be useful to determine whether changes in protein levels correlated with changes in mRNA levels …….

We performed qPCR analysis of Stac3 and Cacna1s in EDL, Soleus and EOM from WT mice (see Figure 1 below). The expression of transcripts encoding Cacna1s and Stac3 is approximately 9-fold higher in EDL compared to Soleus. The fold change of Stac3 and Cacna1s transcripts in EDL muscles is higher compared to the differences we observed by Mass spectrometry at the protein level between EDL and Soleus. Indeed, we found that the content of the Stac3 protein in EDL is 3-fold higher compared to that in soleus. Although there is no apparent linear correlation between mRNA and protein levels, we believe that a few plausible conclusions can be drawn, namely: (i) the expression level of both transcripts and proteins is higher EDL compared to EOM and soleus muscles, respectively, (ii) the expression level of transcripts encoding Stac3 correlate with those encoding Cacan1s and confirm proteomic data. In addition, the level of Stac3 transcript does not changes between WT and dHT, confirming our proteomic data which show that Stac3 protein content in muscles from dHT is similar to that found in WT littermates. Altogether these results support the concept that the differences in Stac3 content between EDL and soleus occur at both the protein and transcript levels, namely high Stac3 mRNA level correlates with higher protein content (EDL) and low mRNA levels correlated with low Stac3 protein content in Soleus muscles (see Figure 1 below).

Figure 2: qPCR of Cacna1s and Stac3 in muscles from WT mice. The expression levels of the transcripts encoding Cacna1s and Stac3 are the highest in EDL muscles and the lowest in soleus muscles (top panels). There are no significant changes in their relative expression levels in dHT vs WT. Each symbol represents the value from of a single mouse. * p=0.028 Mann Whitney test qPCR was performed as described in Elbaz et al., 2019 (Hum Mol Genet 28, 2987-2999).

….and whether or not the protein present was functional, and whether Stac3 was in fact stoichiometrically depleted in relation to Cacna1s.

We thought about this point but think that there are no plausible arguments to believe that Stac3 is not functional, one simple reason being that our WT mice do not have a phenotype which would be associated with the absence of Stac3 (Reinholt et al., PLoS One 8, e62760 2013, Nelson et al. Proc. Natl. Acad. Sci. USA 110:11881 2013).

b) In the abstract, the authors stated that skeletal muscle is responsible for voluntary movement. It is also responsible for non-voluntary. The abstract needs to be refocused on the mutation and on what we learn from this study. Please avoid vague statements like "we provide important insights to the pathophysiological mechanisms..." mainly when the study is descriptive and not mechanistic.

The abstract of the revised manuscript has been rewritten. In particular, we removed statements referring to important “pathophysiological mechanistic insight”.

c) The author should bring up the mutation name, location and phenotype early in the introduction.

In the revised manuscript we provide the information requested by the Reviewer (page 2 lines 36-38 and page 4, lines 98-102).

d) This reviewer also suggests that the authors refocus the introduction on the mutation location in the 3D RyR1 structure (available cryo-EM structure), if there is any nearby ligand binding site, protomers junction or any other known interacting protein partners. This will help the reader to understand how this mutation could be important for the channel's function

The residue Ala4329 is present inside the TMx (Auxiliary transmembrane helices) domain which spans from residue 4322 to 4370 and interposes structurally (des Georges A et al. 2016 Cell 167,145-57; Chen W, et al. 2020 EMBO Rep. 21, e49891). Although the structural resolution of the region has been improved (des Georges et al, 2016), parts of the domain still remain with no defined atomic coordinates, especially the region encompassing a.a. E4253 – F4540. Because of such undefined atomic coordinates of the region E4253-F4540, we are not able to determine the real orientation and the disposition of the amino acids in this region, including the A4329 residue. As reference, structure PDB: 5TAL of des Georges et al, 2016 was analyzed with UCSF Chimera (production version 1.16) (Pettersen et al. J. Comput. Chem. 25: 1605-1612. doi: 10.1002/jcc.20084).

Author Response:

Reviewer #1 (Public Review):

In this study, Kuppan, Mitrovich, and Vahey investigated the impact of antibody specificity and virus morphology on complement activation by human respiratory syncytial virus (RSV). By quantifying the deposition of components of the complement system on RSV particles using high-resolution fluorescence microscopy, they found that antibodies that bind towards the apex of the RSV F protein in either the pre- or post-fusion conformation activated complement most efficiently. Additionally, complement deposition was biased towards globular RSV particles, which were frequently enriched in F in the post-fusion conformation compared to filamentous particles on which F exists predominantly in the pre-fusion conformation.

Strengths:

1) While many previous studies have examined the properties of antibodies that impact Fc-mediated effector functions, this study offers a conceptual advance in its demonstration that heterogeneity in virus particle morphology impacts complement activation. This novel finding will motivate further research on this topic both in the context of RSV and other viral infections.

2) The use of site-specific labeling of viral proteins and high-resolution fluorescence microscopy represents a technical advance in monitoring interactions among different components of antiviral immune responses at the level of single virus particles.

3) The paper is well written, data are clearly presented and support key claims of the paper with caveats appropriately acknowledged.

We appreciate the reviewer’s supportive comments. In our revised manuscript, we have focused on improving clarity regarding the minor weaknesses noted below.

Minor weaknesses:

Working models and their implications could be clarified and extended. Specifically:

1) The finding that globular particles enriched in F proteins in the post-fusion conformation (Fig 3F) are dominant targets of complement activation as measured by C3 deposition by not only post-F- but also pre-F-specific antibodies (Fig 4B, left) is interesting. This is despite the fact that, as expected, pre-F antibodies bind less efficiently to globular particles (Fig 4B, right). How do the authors reconcile these observations, given that C3 deposition seems to be IgG-concentration-dependent (Fig 2E)?

The reviewer raises an excellent point: globular particles, which accumulate as the virus ages, contain more post-F and less pre-F than particles that have recently been shed from infected cells. These ‘aged’ particles nonetheless accumulate more C3 when incubated with pre-F mAbs than ‘younger’ particles, where the proportion of pre-F is higher. We attribute this to the lower surface curvature of globular particles: they accumulate more C3 in the presence of pre-F mAbs in spite of the reduced availability of pre-F epitopes. Figure 1C and 1F help to support this point. This data shows C3 deposition driven by different antibodies bound to particles enriched in either pre-F (Figure 1C) or post-F (Figure 1F). Importantly, for this experiment the conversion to post-F was driven in such a way that virion morphology is preserved (Figure 1E). In this case, we see a clear reduction in C3 deposition by pre-F mAbs on post-F particles (e.g. for CR9501, the percentage of C3-positive particles drops from 24% on pre-F virus to 6% on post-F-enriched virus). This demonstrates that, in the absence of other changes, conversion of pre-F to post-F reduces complement deposition by pre-F specific mAbs.

Similarly, the reviewer correctly points out that reduced levels of antibody binding lead to lower levels of C3 deposition (Figure 2E); however, as in Figure 1, this data is collected from particles with the same morphologies. Thus, in the absence of additional factors, reduction in mAbs bound to pre-F leads to a reduction in C3 deposition driven by these mAbs. The fact that we observe the opposite trend when changes in particle morphology accompany changes in post-F abundance points to an important role for particle shape in activation of the classical pathway.

2) Based on data in Figure 5-figure supplement 2, the authors argue that "large viruses are poised to evade complement activation when they emerge from cells as highly-curved filaments, but become substantially more susceptible as they age or their morphology is physically disrupted." Could the increase in C3 deposition be alternatively explained by a higher density of F proteins on larger particles instead of / in addition to a larger potential decrease in membrane curvature?

We agree that the density of F on a virus – the number of F trimers per unit surface area - likely contributes to the efficiency of C3 deposition. In Figure 6 – figure supplement 2 (Figure 5 – figure supplement 2 in the original submission), we control for this potential effect by comparing viruses that have the same amount of F (as measured by fluorescence intensities of SrtA-labeled F) that are either in filamentous form or globular form (induced through osmotic swelling). The total amount of F per virus is preserved during swelling, and the membrane surface area will remain constant due to the limited ability of lipid bilayers to stretch7. As a result, the input material for these comparisons is the same in terms of F trimers per unit area, yet the C3:F ratio differs substantially. This leads us to conclude that the differences must be attributable to factors other than the density of F. Importantly, this does not mean that the amount of F per unit surface area does not matter for C3 deposition – only that this is not the effect we are observing here. We have added text (Line 299) to help clarify this point: “This effect is unlikely to arise due to changes in the abundance or density of F in the viral membrane, both of which will remain constant following swelling. Similarly, it does not appear to be purely related to size, as larger viral filaments show similar C3:F ratios as smaller viral filaments.”

3) In the discussion, the authors acknowledge that the implications based on the findings are speculative. However, more clarity on the basis of these speculative models would be useful. For example, it is not clear how the findings directly inform the presented model of immunodominance hierarchies in infants.

We agree that this was unclear in the original manuscript. We have rewritten paragraph 4 of the Discussion to clarify how our results may contribute to the changes in immunodominance that have been observed in RSV between infants and adults.

Reviewer #2 (Public Review):

This is an intriguing study that investigates the role of virus particle morphology on the ability of the first few components in the complement pathway to bind and opsonize RSV virions. The authors use primarily fluorescence microscopy with fluorescently tagged F proteins and fluorescently labeled antibodies and complement proteins (C3 and C4). They observed that antibodies against different epitopes exhibited different abilities to induce C3 binding, with a trend reflecting positioning of IgG Fc more distal to the viral membrane resulting in better complement "activation". They also compared the ability of C3 to deposit on virus produced from cells +/- CD55, which inhibits opsonization, and showed knockout led to greater C3 binding, indicating a role for this complement "defense protein" in RSV opsonization. They also examined kinetics of complement protein deposition (probed by C4 binding) to globular vs filamentous particles, observing that deposition occurred more rapidly to non-filaments.

A better understanding of complement activation in response to viruses can lead to a more comprehensive understanding of the immune response to antigen both beneficial and detrimental, when dysfunctional, during infection as well as mechanisms of combating the viral infection. The study provides new mechanistic information for understanding the properties of an enveloped virus that can influence complement activation, at least in an in vitro setting. It remains to be determined whether these effects manifest in the considerably more complex setting of natural infection or even in the presence of a polyclonal antibody mixture.

The studies are elegantly designed and carefully executed with reasonable checks for reproducibility and controls, which is important especially in a relatively complex and heterogeneous experimental system.

We thank the reviewer for the insightful comments. We have revised the manuscript to help to clarify points of confusion and to address some of the technical points raised here.

Specific points:

1) "Complement activation" involves much more than C3 or C4 binding. Better to use more specific terminology relating to the observable (i.e. fluorescently labeled complement component binding)

We agree with the reviewer. We have revised the manuscript throughout to make our language more accurate and precise.

2) What is the rationalization for concentrations of antibodies used? What range was tested, and how dependent on antibody concentration were the observed complement deposition trends? How do they relate to physiological concentrations, and how would the presence of a more complex polyclonal response that is typically present (e.g. as the authors noted, the serum prior to antibody depletion already mediates complement activation) affect the complement activation trends? The neat, uniform display of Fc for monoclonals that were tested is likely to be quite garbled in more natural antibody response situations. This should be discussed.

We have added discussion of antibody concentrations and possible differences between monoclonal and polyclonal responses to the revised manuscript. Below, we address the specific questions raised here by the reviewer.

We chose to use antibody concentrations that are comparable to the concentrations of dominant clonotypes in post-vaccination serum1. Our goal in selecting relatively high antibody concentrations for our experiments was to focus on understanding the capacity of an antibody to drive complement deposition when it has reached maximum densities on RSV particles. This is discussed starting on Line 125 of Results, and in paragraph 2 of Discussion. Experiments testing a range of antibody concentrations would be valuable, but are likely to strongly reflect differences in the binding affinities of these antibodies, which have been characterized previously.

Although we have not performed titrations for each of the antibodies tested due to the large number of conditions needed and the limited throughput of our experimental approach, the manuscript does present a dilution series for CR9501, the IgG1 mAb with the greatest potency in driving C3 deposition among those tested here. This data (shown in Figure 3E & F in the revised manuscript) shows that as the amount of antibody added in solution decreases over a 16-fold range, C3 deposition decreases as well. The decrease in C3 deposition is roughly commensurate with the reduction in antibody binding, reaching levels that are just above background at an antibody concentration of ~0.6μg/ml (1:800 dilution). We think it is likely that other activating antibodies would show similar trends, while antibodies that do not activate the classical pathway at saturating concentrations would be unlikely to do so across a range of lower concentrations.

We agree with the reviewer that complement deposition driven by polyclonal antibodies is more complex than the monoclonal responses studied here. As discussed in paragraph 2 of our revised Discussion, one effect that polyclonal serum might have is to increase the density of Fcs on the virus by providing antibody mixtures that bind to multiple non-overlapping antigenic sites. We speculate that this would generally increase complement deposition, provided that sufficient antibodies are present that bind to productive antigenic sites (e.g. sites 0/ , II, and V).

Finally, we note that we observe a similar phenomenon where globular particles are preferentially opsonized with C3 in our experiments with polyclonal serum where IgG and IgM have not been depleted (Figure R1). The major limitation of this data – which is resolved by using monoclonal antibodies – is the difficulty of determining to what extent this bias arises due to the epitopes targeted by the polyclonal serum versus the intrinsic sensitivity of the virus particles.

Figure R1: RSV opsonized with polyclonal human serum. A similar bias towards globular particles (white dashed circles) is observed as in experiments with monoclonal antibodies.

3) Are there artifacts or caveats resulting from immobilization of virus particles on the coverslips?

As pointed out by the reviewer, a few possible artifacts or caveats could arise due to the immobilization of viruses on coverslips. These include (1) spurious binding of C1 or other complement components to the immobilizing antibody (3D3); (2) reduced access to viral antigens as a result of immobilization; and (3) inhibition of antibody-induced viral aggregation. We are able to rule out issues associated with (1), because we do not see attachment of C1 or C3 to the coverslip (i.e. outside regions occupied by virus particles). This is consistent with the fact that the antibodies are immobilized on the surface via a C-terminal biotin attached to the heavy chain, which would limit access for C1 binding and prevent the formation of Fc hexamers.

Immobilization on coverslips could reduce the accessibility of a portion of the virus for binding by antibodies and complement proteins. This could effectively shield a portion of the viral surface from assembly of an activating complex, which we estimate requires ~35nm of clearance above the targeted epitope on F8. Importantly, the fraction of the viral surface area that would be shielded would vary for filaments and spheres; to determine if this could influence our results, we calculated the expected magnitude of this effect (Figure R2). To do this, we modeled the virus as being tethered to the surface via a 25nm linkage. This accounts for the length of the biotinylated PEG (~5-15nm for PEG2K, depending on the degree of extension), streptavidin (~5nm), and the anti-G antibody (~10-15nm including the biotinylated C-terminal linker). Although limited structural information is available for RSV G, the ~100 residue, heavily glycosylated region between the viral membrane and the 3D3 epitope likely extends above the height of F (~12nm). Our model assumes that a shell of thickness d surrounding the virus is necessary for antibody-C1 complexes to fit without clashing with the surface (this shell is shaded in gray in the schematic from Figure R2). Tracing the angles at which this shell clashes with the coverslip allows us to calculate the fraction of total surface area that is inaccessible for activation of the classical pathway. The results are plotted on the right side of Figure R2. The relative surface area accessible to a 35nm activating antibody-C1 complex differs between a filament and a sphere of equivalent surface area by about 15%. We conclude that this difference is modest compared to the ~5-fold difference in deposition kinetics we observe between viral filaments and spheres (Figure 4), or the 3- to 10-fold difference in relative C3 deposition we observe on larger filamentous particles after conversion to spheres (Figure 6 – figure supplement 2C).

Finally, by performing experiments on immobilized viruses, we eliminate the possibility for antibody-dependent particle aggregation. While this was necessary for us to get interpretable results, the formation of viral aggregates could affect the dynamics and extent of complement deposition. For example, activation of the classical pathway on one particle in an aggregate could spread to non-activating particles through a “bystander effect”, as has been reported in other contexts9. We are interested in this question and have begun preliminary experiments in this direction; however, we believe that a definitive answer is outside the scope of this current work. To alert readers to this consideration, we have added this to paragraph 2 of the revised Discussion (Line 359).

Figure R2: Estimating the surface accessibility of RSV particles bound to coverslips. Definition of variables: af: radius of cylindrical RSV filament; as: radius of spherical RSV particle of equivalent surface area (see Figure 6 – figure supplement 2A); d: distance needed above the viral surface to accommodate IgG-C1 activating complexes; h: height of viral surface above the coverslip; L: length of the viral filament.

4) How is the "density of antigen" quantitated? What fraction of F or G is labeled? For fluorescence intensity measurements in general, how did the authors ensure their detection was in a linear sensitivity range for the detectors for the various fluorescent channels? Since quantitation of fluorescence intensities is important in this study, some discussion in methods would be valuable.

We have performed this important additional characterization of our fluorescence system and our overall labeling and quantification strategy to address these concerns. The results of this characterization are now included in two new figure supplements in the revised manuscript (Figure 1 – figure supplements 2 & 3).

5) The authors also show that the particle morphology, whether globular or filamentous, as well as relative size and resulting apparent curvature, correlate with ability of C3 to bind. Some link to the abundance of post-fusion F (post-F) is examined and discussed, but I found the back and forth discussion between morphology, C3 binding, and post-F abundance to be confusing and in need of clarification and streamlining. Is there a mechanistic link between morphology changes and post-F level increases? Are the two linked or coincidental (for example does pre-F interaction with matrix help stabilize that conformation, and if lost lead to spontaneous conversion to post-F?). Please clarify.

Specifically, we have separated the discussion of pre-F versus post-F abundance and particle morphology into two different sections in Results, and we have rearranged Figures 4 and 5 (Figures 3 and 4 in the original submission) to improve clarity.

Regarding the question of whether changes in morphology and the pre-F to post-F conversion are coincidental or mechanistically linked: the answer is not entirely clear, although we have collected new data that suggests a connection. We first want to note that the two effects are at least partly separable: brief treatment with a low osmolarity solution causes particle shape to change while preserving pre-F (Figure 6A & B), whereas treating with an osmotically balanced solution with low ionic strength converts pre-F to post-F without affecting virus shape (Figure 1E). However, we were motivated by the reviewer’s questions to look into this further. To determine if the change in viral shape may serve to destabilize the pre-F conformation over time, we compared the relative amounts of pre-F and post-F present in particles that were osmotically swollen to those that were not at 0h and at 24h. In these experiments, particles were swollen using a brief (~1 minute) exposure to low osmolarity conditions before returning them to PBS (Figure R3, left). As expected, we observe no immediate change in pre-F abundance following the brief osmotic shock (Figure R3, right: 0h time point), consistent with Figure 6B. After incubating the particles an additional 24h at 37oC, the post-F-to-pre-F ratio is ~3.5-fold higher in osmotically-swollen particles than in those where filamentous morphology was initially preserved (Figure R3, right: 24h time point). This supports the reviewer’s suggestion that interactions with the matrix may help to stabilize F in the prefusion conformation, since the conversion to post-F is faster when this interaction is disrupted. Whether or not this has any relevance for RSV entry into cells remains to be determined; however, it is worth noting that we observed no clear loss or gain of infectivity in RSV particles following osmotic swelling (Figure 6 – figure supplement 1A). Since this result may be of interest to readers, we have included this new data in Figure 6 – figure supplement 1B, and it is discussed briefly in Results (Line 250).

Figure R3: Determining stability of pre-F following matrix detachment. Left: Experimental design. Right: Comparison of pre-F stability on untreated particles (gray) and particles subjected to brief osmotic swelling (magenta). Distributions show the ratio of post-F (ADI-14353) to pre-F (5C4) intensities per particle, combined for four biological replicates, sampled at 0h (immediately after swelling) and after an additional incubation at 37oC for 24h. Black points show median values for each individual replicate. P-values are determined from a two-sample T test.

6) Since their conclusion is that curvature of the virus surface is a major influence on the ability of complement proteins to bind, I feel that some effort at modeling this effect based upon known structures is warranted. One might also anticipate then that there would be some epitope-dependent effect as a result of changes in curvature that may lead to an exaggeration of the epitope-specific effects for more highly curved particles perhaps than those with lower curvature? Is this true?

The reviewer raises two excellent points: that it may be possible to gain insight into the mechanisms through which curvature dictates C1 binding and other aspects of complement activation through structural modeling, and that such a model may help to identify specific epitope effects that could contribute to curvature dependence.

We developed simulations based on the geometry of RSV, F, and hexameric IgG to try to better understand how curvature may influence initiation of the classical pathway. This model is described in the Methods section (Modeling IgG hexamers on curved surfaces), and the results are discussed in the final two paragraphs of the Results section. In addition, we have included a new figure (Figure 7) to summarize the model’s predictions. This model corroborates the curvature sensitivity of IgG hexamer formation and suggests a possible intuitive explanation for our findings: high curvature effectively increases the distance between epitopes that sit high above the viral membrane, decreasing the likelihood of hexamer formation (Figure 7D). Regarding epitope specific effects, this model suggests that the further the epitope is above the viral membrane, the greater the effect that decreasing curvature will have. However, we find that epitopes closer to the membrane (e.g. those bound by 101F or ADI-19425) are overall very inefficient at activating the classical pathway, potentially due to steric obstruction of the formation of IgG hexamers. Thus, there may be an inherent tradeoff between overcoming steric obstruction (by binding to epitopes distal to the membrane) and sensitivity to surface curvature.

It is important to note that this model is reductionist and does not include detailed structural information. Additional factors may be important for considering epitope-specific effects. For example, antibodies that bind equatorially on F (e.g. ADI-19425, which binds to antigenic site III), show minimal complement deposition in our experiments. However, particles whose curvature approaches the diameter of hexameric IgG or IgM (~20nm) may display these epitopes in a manner that is more accessible. If the curvature necessary to observe such an effect falls outside of the biologically accessible range, it would not be observable in our experiments. Nonetheless, it is possible that a different set of antibodies may drive complement deposition on highly-curved nanoparticle vaccines that are in development10. We have added this important point to the second paragraph of the Discussion.

7) Line 265: it would be useful to confirm the increase C1 binding as a function of morphology as was done for antibody-angle of binding experiments.

We believe that this data is shown in Figure 6B (Figure 5B in the original manuscript).

Reviewer #3 (Public Review):

Overall the manuscript is clearly written and the data are displayed well, with helpful diagrams in the figures to illustrate assays and RSV F epitopes. The engineering of the RSV strain to include a fluorescent reporter and tags on F and G that serve as substrates for fluorophore attachment is impressive and is a strength. The RSV literature is well cited and the interpretation of the results is consistent with structure/function data on RSV F and its interaction with antibodies. This reviewer is not an expert on the experiments performed in this manuscript, but they appear to be rigorously performed with appropriate controls. As such, the conclusions are justified by the data. One weakness is the extent to which the results regarding virion morphology are biologically relevant. Non-filamentous forms of the virion are generally obtained only in vitro as a result of virion purification or biochemical treatment. However, these results may be relevant for certain vaccine candidates, including the failed formalin-inactivated RSV vaccine that was evaluated in the late 1960s and caused vaccine-enhanced disease upon natural RSV infection.

Thank you for these suggestions, which have helped us to better place our results regarding RSV morphology in the context of prior work. We agree with the reviewer that non-filamentous RSV particles are commonly obtained in vitro, and that this morphology does not reflect the structure of the virus as it is budding from infected cells. Our work has characterized the transition from filament to globular / amorphous form, with the finding that it can occur rapidly upon physical or chemical perturbations, as well as more gradually during natural aging: i.e. in the absence of handling or purification. We are also able to detect globular particles accumulating in cultured A549 cells, where no handling has occurred prior to observation (Figure 5 – figure supplement 1). While we do not currently know how well this reflects the tendency of RSV to undergo conversion from filament to sphere in vivo, we propose that it is plausible that such a transformation could occur. To distinguish between what we demonstrate and what we speculate, we write (Line 401): “Although more work is needed to understand the prevalence of globular particles during in vivo infection, our observations that these particles accumulate over time through the conversion of viral filaments – even under normal cell culture conditions - suggest that their presence in vivo is feasible, where the physical and chemical environment would be considerably harsher and more complex.”

We agree with the reviewer that our results may have relevance towards understanding the failed formalin-inactivated vaccine trial. We have added this to paragraph 5 of the Discussion section.

Author Response

Public Evaluation Summary:

The authors re-analyzed a previously published dataset and identify patterns suggestive of increased bacterial biodiversity in the gut may creating new niches that lead to gene loss in a focal species and promote generation of more diversity. Two limitations are (i) that sequencing depth may not be sufficient to analyze strain-level diversity and (ii) that the evidence is exclusively based on correlations, and the observed patterns could also be explained by other eco-evolutionary processes. The claims should be supported by a more detailed analysis, and alternative hypotheses that the results do not fully exclude should be discussed. Understanding drivers of diversity in natural microbial communities is an important question that is of central interest to biomedically oriented microbiome scientists, microbial ecologists and evolutionary biologists.

We agree that understanding the drivers of diversity in natural communities is an important and challenging question to address. We believe that our analysis of metagenomes from the gut microbiomes is complementary to controlled laboratory experiments and modeling studies. While these other studies are better able to establish causal relationships, we rely on correlations – a caveat which we make clear, and offer different mechanistic explanations for the patterns we observe.

We also mention the caveat that we are only able to measure sub-species genetic diversity in relatively abundant species with high sequencing depth in metagenomes. These relatively abundant species include dozens of species in two metagenomic datasets, and we see no reason why they would not generalize to other members of the microbiome. Nonetheless, further work will be required to extend our results to rarer species.

Our revised manuscript includes two major new analyses. First, we extend the analysis of within-species nucleotide diversity to non-synonymous sites, with generally similar results. This suggests that evolutionarily older, less selectively constrained synonymous mutations and more recent non-synonymous mutations that affect protein structure both track similarly with measures of community diversity – with some subtle differences described in the manuscript.

Second, we extend our analysis of dense time series data from one individual stool donor and one deeply covered species (B. vulgatus) to four donors and 15 species. This allowed us to reinforce the pattern of gene loss in more diverse communities with greater statistical support. Our correlational results are broadly consistent with the predictions of DBD from modeling and experimental studies, and they open up new lines of inquiry for microbiome scientists, ecologists, and evolutionary biologists.

Reviewer #1 (Public Review):

This paper makes an important contribution to the current debate on whether the diversity of a microbial community has a positive or negative effect on its own diversity at a later time point. In my view, the main contribution is linking the diversity-begets-diversity patterns, already observed by the same authors and others, to genomic signatures of gene loss that would be expected from the Black Queen Hypothesis, establishing an eco-evolutionary link. In addition, they test this hypothesis at a more fine-grained scale (strain-level variation and SNP) and do so in human microbiome data, which adds relevance from the biomedical standpoint. The paper is a well-written and rigorous analysis using state-of-the-art methods, and the results suggest multiple new experiments and testable hypotheses (see below), which is a very valuable contribution.

We thank the reviewer for their generous comments.

That being said, I do have some concerns that I believe should be addressed. First of all, I am wondering whether gene loss could also occur because of environmental selection that is independent of other organisms or the diversity of the community. An alternative hypothesis to the Black Queen is that there might have been a migration of new species from outside and then loss of genes could have occurred because of the nature of the abiotic environment in the new host, without relationship to the community diversity. Telling the difference between these two hypotheses is hard and would require extensive additional experiments, which I don't think is necessary. But I do think the authors should acknowledge and discuss this alternative possibility and adjust the wording of their claims accordingly.

We concur with the reviewer that the drivers of the correlation between community diversity and gene loss are unclear. Therefore, we have now added the following text to the Discussion:

“Here we report that genome reduction in the gut is higher in more diverse gut communities. This could be due to de novo gene loss, preferential establishment of migrant strains encoding fewer genes, or a combination of the two. The mechanisms underlying this correlation remain unclear and could be due to biotic interactions – including metabolic cross-feeding as posited by some models (Estrela et al., 2022; San Roman and Wagner, 2021, 2018) but not others (Good and Rosenfeld, 2022) – or due to unknown abiotic drivers of both community diversity and gene loss.”

Additionally, we have revised Figure 1 to show that strain invasions/replacements, in addition to evolutionary change, could be an important driver of changes in intra-species diversity in the microbiome.

Another issue is that gene loss is happening in some of the most abundant species in the gut. Under Black Queen though, we would expect these species to be most likely "donors" in cross-feeding interactions. Authors should also discuss the implications, limitations, and possible alternative hypotheses of this result, which I think also stimulates future work and experiments.

We thank the reviewer for raising this point. It is unclear to us whether the more abundant species would be donors in cross-feeding interactions. If we understand correctly, the reviewer is suggesting that more abundant donors will contribute more total biomass of shared metabolites to the community. This idea makes sense under the assumption that the abundant species are involved in cross-feeding interactions in the first place, which may or may not be the case. As our work heavily relies on a dataset that we previously analyzed (HMP), we wish to cite Figure S20 in Garud, Good et al. 2019 PLoS Biology in which we found there are comparable rates of gene changes across the ~30 most abundant species analyzed in the HMP. This suggests that among the most abundant species analyzed, there is no relationship between their abundance and gene change rate.

That being said, we acknowledge that our study is limited to the relatively abundant focal species and state now in the Discussion: “Deeper or more targeted sequencing may permit us to determine whether the same patterns hold for rarer members of the microbiome.”

Regarding Figure 5B, there is a couple of questions I believe the authors should clarify. First, How is it possible that many species have close to 0 pathways? Second, besides the overall negative correlation, the data shows some very conspicuous regularities, e.g. many different "lines" of points with identical linear negative slope but different intercept. My guess is that this is due to some constraints in the pathway detection methods, but I struggle to understand it. I think the authors should discuss these patterns more in detail.

We sincerely thank the reviewer for raising this issue, as it prompted us to investigate more deeply the patterns observed at the pathway level. In short, we decided to remove this analysis from the paper because of a number of bioinformatics issues that we realized were contributing to the signal. However, in support of BQH-like mechanisms at play, we do find evidence for gene loss in more diverse communities across multiple species in both the HMP and Poyet datasets. Below we detail our investigation into Figure 5b and how we arrived at the conclusion that is should be removed:

(1) Regarding data points in Figure 5B where many focal species have “zero pathways”,we firstly clarify how we compute pathway presence and richness. Pathway abundance data per species were downloaded from the HMP1-2 database, and these pathway abundances were computed using HUMAnN (HMP Unified Metabolic Analysis Network). According to HUMAnN documentation, pathway abundance is proportional to the number of complete copies of the pathway in the community; this means that if at least one component reaction in a certain pathway is missing coverage (for a sample-species pair), the pathway abundance may be zero (note that HUMAnN also employs “gap filling” to allow no more than one required reaction to have zero abundance). As such, it is likely that insufficient coverage, especially for low-abundance species, causes many pathways to report zero abundance in many species in many samples. Indeed, 556 of the 649 species considered had zero “present” pathways (i.e. having nonzero abundance) in at least 400 of the 469 samples (see figure below).

(2) We thank the reviewer for pointing out the “conspicuous regularities” in Figure 5B,particularly “parallel lines” of data points that we discovered are an artifact of the flawed way in which we computed “community pathway richness [excluding the focal species].” Each diagonal line of points corresponds to different species in the same sample, and because community pathway richness is computed as the total number of pathways [across all species in the sample] minus the number of pathways in the focal species, the current Figure 5B is really plotting y against X-y for each sample (where X is a sample’s total community pathway richness, and y is the pathway richness of an individual species in that sample). This computation fails to account for the possibility that a pathway in an excluded focal species will still be present in the community due to redundancy, and indeed BQH tests for whether this redundancy is kept low in diverse communities due to mechanisms such as gene loss.

We attempted to instead plot community pathway richness defined as the number of unique pathways covered by all species other than the focal species. This is equivalent to [number of unique pathways across all species in a sample] minus the [number of pathways that are ONLY present in the focal species and not any other species in the sample]. However, when we recomputed community pathway richness this way, it is rare that a pathway is present in only one species in a sample. Moreover, we find that with the exception of E. coli, focal species pathway richness tended to be very similar across the 469 samples, often reaching an upper limit of focal species pathway richness observed. (It is unclear to what extent lower pathway richnesses are due to low species abundance/low sample coverage versus gene loss). This new plot reveals even more regularities and is difficult to interpret with respect to BQH. (Note that points are colored by species; the cluster of black dots with outlying high focal pathway richness corresponds to the “unclassified” stratum which can be considered a group of many different species.)

Overall, because community pathway richness (excluding a focal species) seems to primarily vary with sample rather than focal species in this dataset when using the most simple/strict definition of community pathway richness as described above, it is difficult to probe the Black Queen Hypothesis using a plot like Figure 5B. As pointed out by reviewers, lack of sequencing depth to analyze strain-level diversity and accurately quantify pathway abundance, irrespective of species abundance, seems to be a major barrier to this analysis. As such, we have decided to remove Figure 5B from the paper and rewrite some of our conclusions accordingly.

Finally, I also have some conceptual concerns regarding the genomic analysis. Namely, genes can be used for biosynthesis of e.g. building blocks, but also for consumption of nutrients. Under the Black Queen Hypothesis, we would expect the adaptive loss of biosynthetic genes, as those nutrients become provided by the community. However, for catabolic genes or pathways, I would expect the opposite pattern, i.e. the gain of catabolic genes that would allow taking advantage of a more rich environment resulting from a more diverse community (or at least, the absence of pathway loss). These two opposing forces for catabolic and biosynthetic genes/pathways might obscure the trends if all genes are pooled together for the analysis. I believe this can be easily checked with the data the authors already have, and could allow the authors to discuss more in detail the functional implications of the trends they see and possibly even make a stronger case for their claims.

We thank the reviewer for their suggestion. As explained above, we have removed the pathway analysis from the paper due to technical reasons. However, we did investigate catabolic and biosynthetic pathways separately as suggested by the reviewer as we describe below:

We obtained subsets of biosynthetic pathways and catabolic pathways by searching for keywords (such as “degradation” for catabolic) in the MetaCyc pathway database. After excluding the “unclassified” species stratum, we observe a total of 279 biosynthetic and 167 catabolic pathways present in the HMP1-2 pathway abundance dataset. Using the corrected definition of community pathway richness excluding a focal species, for each pathway type—either biosynthetic or catabolic—we plotted focal species pathway richness against community pathway richness including all pathways regardless of type:

We observe the same problem where, within a sample, community pathway richness excluding the focal species hardly varies no matter which focal species it is, due to nearly all of its detected pathways being present in at least one other species; this makes the plots difficult to interpret.

Reviewer #2 (Public Review):

The authors re-analysed two previously published metagenomic datasets to test how diversity at the community level is associated with diversity at the strain level in the human gut microbiota. The overall idea was to test if the observed patterns would be in agreement with the "diversity begets diversity" (DBD) model, which states that more diversity creates more niches and thereby promotes further increase of diversity (here measured at the strain-level). The authors have previously shown evidence for DBD in microbiomes using a similar approach but focusing on 16S rRNA level diversity (which does not provide strain-level insights) and on microbiomes from diverse environments.

One of the datasets analysed here is a subset of a cross-sectional cohort from the Human Microbiome Project. The other dataset comes from a single individual sampled longitudinally over 18 months. This second dataset allowed the authors to not only assess the links between different levels of diversity at single timepoints, but test if high diversity at a given timepoint is associated with increased strain-level diversity at future timepoints.

Understanding eco-evolutionary dynamics of diversity in natural microbial communities is an important question that remains challenging to address. The paper is well-written and the detailed description of the methodological approaches and statistical analyses is exemplary. Most of the analyses carried out in this study seem to be technically sound.

We thank the reviewer for their kind words, comments, and suggestions.

The major limitation of this study comes with the fact that only correlations are presented, some of which are rather weak, contrast each other, or are based on a small number of data points. In addition, finding that diversity at a given taxonomic rank is associated with diversity within a given taxon is a pattern that can be explained by many different underlying processes, e.g. species-area relationships, nutrient (diet) diversity, stressor diversity, immigration rate, and niche creation by other microbes (i.e. DBD). Without experiments, it remains vague if DBD is the underlying process that acts in these communities based on the observed patterns.

We thank the reviewer for their comments. First, regarding the issue of this being a correlative study, we now more clearly acknowledge that mechanistic studies (perhaps in experimental settings) are required to fully elucidate DBD and BQH dynamics. However, we note that our correlational study from natural communities is complementary to experimental and modeling studies, to test the extent to which their predictions hold in more complex, realistic settings. This is now mentioned throughout the manuscript, most explicitly at the end of the Introduction:

“Although such analyses of natural diversity cannot fully control for unmeasured confounding environmental factors, they are an important complement to controlled experimental and theoretical studies which lack real-world complexity.”

Second, to increase the number of data points analyzed in the Poyet study, we now include 15 species and four different hosts (new Figure 5). The association between community diversity and gene loss is now much more statistically robust, and consistent across the Poyet and HMP time series.

Third, we acknowledge more clearly in the Discussion that other processes, including diet and other environmental factors can generate the DBD pattern. We also now stress more prominently the possibility that strain migration across hosts may be responsible for the patterns observed. For example, in Figure 1, we illustrate the possibility of strain migration generating the patterns we observe.

Below we quote a paragraph that we have now added in the Discussion:

"Second, we cannot establish causal relationships without controlled experiments. We are therefore careful to conclude that positive diversity slopes are consistent with the predictions of DBD, and negative slopes with EC, but unmeasured environmental drivers could be at play. For example, increased dietary diversity could simultaneously select for higher community diversity and also higher intra-species diversity. In our previous study, we found that positive diversity slopes persisted even after controlling for potential abiotic drivers such as pH and temperature (Madi et al., 2020), but a similar analysis was not possible here due to a lack of metadata. Neutral processes can account for several ecological patterns such as species-area relationships (Hubbell, 2001), and must be rejected in favor of niche-centric models like DBD or EC. Using neutral models without DBD or EC, we found generally flat or negative diversity slopes due to sampling processes alone and that positive slopes were hard to explain with a neutral model (Madi et al., 2020). These models were intended mainly for 16S rRNA gene sequence data, but we expect the general conclusions to extend to metagenomic data. Nevertheless, further modeling and experimental work will be required to fully exclude a neutral explanation for the diversity slopes we report in the human gut microbiome.”

Finally, we now put more emphasis on the importance of migration (strain invasion) as a non-exclusive alternative to de novo mutation and gene gain/loss. This is mentioned in the Abstract and is also illustrated in the revised Figure 1.

Another limitation is that the total number of reads (5 mio for the longitudinal dataset and 20 mio for the cross-sectional dataset) is low for assessing strain-level diversity in complex communities such as the human gut microbiota. This is probably the reason why the authors only looked at one species with sufficient coverage in the longitudinal dataset.

Indeed, this is a caveat which means we can only consider sub-species diversity in relatively abundant species. Nevertheless, this allows us to study dozens of species in the HMP and 15 in the more frequent Poyet time series. As more deeply sequenced metagenomes become available, future studies will be able to access the rarer species to test whether the same patterns hold or not. This is now mentioned prominently as a caveat our study in the second Discussion paragraph:

“First, using metagenomic data from human microbiomes allowed us to study genetic diversity, but limited us to considering only relatively abundant species with genomes that were well-covered by short sequence reads. Deeper or more targeted sequencing may permit us to determine whether the same patterns hold for rarer members of the microbiome. However, it is notable that the majority of the dozens of species across the two datasets analyzed support DBD, suggesting that the phenomenon may generalize.”

We also note that rarefaction was only applied to calculate community richness, not to estimate sub-species diversity. We apologize for this confusion, which is now clarified in the Methods as follows:

“SNV and gene content variation within a focal species were ascertained only from the full dataset and not the rarefied dataset.”

Analyzing the effect of diversity at a given timepoint on strain-level diversity at a later timepoint adds an important new dimension to this study which was not assessed in the previous study about the DBD in microbiomes by some of the authors. However, only a single species was analysed in the longitudinal dataset and comparisons of diversity were only done between two consecutive timepoints. This dataset could be further exploited to provide more insights into the prevailing patterns of diversity.

We thank the reviewer for raising this point. We now have considered all 15 species for which there was sufficient coverage from the Poyet dataset, which included four different stool donors. Additionally, in the HMP dataset, we analyze 54 species across 154 hosts, with both datasets showing the same correlation between community diversity and gene loss.

Additionally, we followed the suggestion of the reviewer of examining additional time lags, and in Figure 5 we do observe a dependency on time. This is now described in the Results as follows:

“Using the Poyet dataset, we asked whether community diversity in the gut microbiome at one time point could predict polymorphism change at a future time point by fitting GAMs with the change in polymorphism rate as a function of the interaction between community diversity at the first time point and the number of days between the two time points. Shannon diversity at the earlier time point was correlated with increases in polymorphism (consistent with DBD) up to ~150 days (~4.5 months) into the future (Figure S4), but this relationship became weaker and then inverted (consistent with EC) at longer time lags (Fig 5A, Table S8, GAM, P=0.023, Chi-square test). The diversity slope is approximately flat for time lags between four and six months, which could explain why no significant relationship was found in HMP, where samples were collected every ~6 months. No relationship was observed between community richness and changes in polymorphism (Table S8, GAM, P>0.05).”

Finally, the evidence that gene loss follows increase in diversity is weak, as very few genes were found to be lost between two consecutive timepoints, and the analysis is based on only a single species. Moreover, while positive correlation were found between overall community diversity and gene family diversity in single species, the opposite trend was observed when focusing on pathway diversity. A more detailed analysis (of e.g. the functions of the genes and pathways lost/gained) to explain these seemingly contrasting results and a more critical discussion of the limitations of this study would be desirable.

We agree that our previous analysis of one species in one host provided weak support for gene loss following increases in diversity. As described in the response above, we have now expanded this analysis to 15 focal species and 4 independent hosts with extensive time series. We now analyze this larger dataset and report the more statistically robust results as follows:

“We found that community Shannon diversity predicted future gene loss in a focal species, and this effect became stronger with longer time lags (Fig 5B, Table S9, GLMM, P=0.006, LRT for the effect of the interaction between the initial Shannon diversity and time lag on the number of genes lost). The model predicts that increasing Shannon diversity from its minimum to its maximum would result in the loss of 0.075 genes from a focal species after 250 days. In other words, about one of the 15 focal species considered would be expected to lose a gene in this time frame.

Higher Shannon diversity was also associated with fewer gene gains, and this relationship also became stronger over time (Fig 5C, Table S9, GLMM, P=1.11e-09, LRT). We found a similar relationship between community species richness and gene gains, although the relationship was slightly positive at shorter time lags (Fig 5D, Table S9, GLMM, P=3.41e-04, LRT). No significant relationship was observed between richness and gene loss (Table S9, GLMM, P>0.05). Taken together with the HMP results (Fig 4), these longer time series reveal how the sign of the diversity slope can vary over time and how community diversity is generally predictive of reduced focal species gene content.”

As described in detail in the response to Reviewer 1 above, we found that the HUMAnN2 pathway analyses previously described suffered from technical challenges and we deemed them inconclusive. We have therefore removed the pathway results from the manuscript.

Reviewer #3 (Public Review):

This work provides a series of tests of hypothesis, which are not mutually exclusive, on how genomic diversity is structured within human microbiomes and how community diversity may influence the evolution of a focal species.

Strengths:

The paper leverages on existing metagenomic data to look at many focal species at the same time to test for the importance of broad eco-evolutionary hypothesis, which is a novelty in the field.

Thank you for the succinct summary and recognition of the strengths of our work.

Weaknesses:

It is not very clear if the existing metagenomic data has sufficient power to test these models.

It is not clear, neither in the introduction nor in the analysis what precise mechanisms are expected to lead to DBD.

The conclusion that data support DBD appears to depend on which statistics to measure of community diversity are used. Also, performing a test to reject a null neutral model would have been welcome either in the results or in the discussion.

In our revised manuscript, we emphasize several caveats – including that we only have power to test these hypotheses in focal species with sufficient metagenomic coverage to measure sub-species diversity. We also describe more in the Introduction how the processes of competition and niche construction can lead to DBD. We also acknowledge that unmeasured abiotic drivers of both community diversity and sub-species diversity could also lead to the observed patterns. Throughout the manuscript, we attempt to describe the results and acknowledge multiple possible interpretations, including DBD and EC acting with different strengths on different species and time scales. Our previous manuscript assessing the evidence for DBD using 16S rRNA gene amplicon data from the Earth Microbiome Project (Madi et al., eLife 2020) assessed null models based on neutral ecological theory, and found it difficult to explain the observation of generally positive diversity slopes without invoking a non-neutral mechanism like DBD. While a new null model tailored to metagenomic data might provide additional nuance, we think developing one is beyond the scope of the manuscript – which is in the format of a short ‘Research Advance’ to expand on our previous eLife paper, and we expect that the general results of our previously reported null model provide a reasonable intuition for our new metagenomic analysis. This is now mentioned in the Discussion as follows:

“In our previous study, we found that positive diversity slopes persisted even after controlling for potential abiotic drivers such as pH and temperature (Madi et al., 2020), but a similar analysis was not possible here due to a lack of metadata. Neutral processes can account for several ecological patterns such as species-area relationships (Hubbell, 2001), and must be rejected in favor of niche-centric models like DBD or EC. Using neutral models without DBD or EC, we found generally flat or negative diversity slopes due to sampling processes alone and that positive slopes were hard to explain with a neutral model (Madi et al., 2020). These models were intended mainly for 16S rRNA gene sequence data, but we expect the general conclusions to extend to metagenomic data. Nevertheless, further modeling and experimental work will be required to fully exclude a neutral explanation for the diversity slopes we report in the human gut microbiome.”

Author Response:

Reviewer #1 (Public Review):

5.The reported data point to an important role of the premotor and parietal regions of the left as compared to the right hemisphere in the control of ipsilateral and contralateral limb movements. These are also the regions where the electrodes were primarily located in both subgroups of patients. I have 2 concerns in this respect. The first concern refers to the specific locus of these electrodes. For premotor cortex, the authors suggest PMd as well as PMv as potential sites for these bilateral representations. The other principal site refers to parietal cortex but this covers a large territory. It would help if more specific subregions for the parietal cortex can be indicated, if possible. Do the focal regions where electrodes were positioned refer to the superior vs inferior parietal cortex (anterior or posterior), or intra-parietal sulcus. Second, the manuscript's focus on the premotor-parietal complex emerges from the constraints imposed by accessible anatomical locations in the participants but does not preclude the existence of other cortical sites as well as subcortical regions and cerebellum for such bilateral representations. It is meaningful to clarify this and/or list this as a limitation of the current approach.

On the first issue, we have updated the manuscript to specify the subregion within the parietal cortex in which we see stronger across-arm generalization - namely, the superior parietal cortex. On the second issue, we have added text in the Discussion that reference subcortical areas shown to exhibit laterality differences in bimanual coordination, providing a more holistic picture of bimanual representations across the brain. In addition, we acknowledge that with our current patient population we are limited to regions with substantial electrode coverage, which does not include all areas of the brain.

6.The evidence for bilateral encoding during unilateral movement opens perspectives for a better understanding of the control of bimanual movements which are abundant during every day life. In the discussion, the authors refer to some imaging studies on bimanual control in order to infer whether the obtained findings may be a consequence of left hemisphere specialization for bimanual movement control, leading to speculations about the information that is being processed for each of both limb movements. Another perspective to consider is the possibility that making a movement with one limb may require postural stabilization in the trunk and contralateral body side, including a contribution from the opposite limb that is supposedly resting on the start button. Have the authors considered whether this postural mechanism could (partly) account for this bilateral encoding mechanism, in particular, because it appears more prominent during movement execution as compared to preparation. Furthermore, could the prominence of bilateral encoding during movement execution be triggered by inflow of sensory information about both limbs from the visual as well as the somatosensory systems.

Thank you for these comments. We have added a paragraph to the Discussion to address the hypothesis that some component of ipsilateral encoding may be related to postural stabilization.

In response to the final point in this comment, we agree that bilateral information during execution could be reflective of afferent inputs (somatosensory and/or visual). However, the encoding model shows that activity in premotor and parietal regions are well predicted based on kinematics during the task. While visual and somatosensory system information are likely integrated in these areas, the kinematic encoding would point to a more movement-based representation.

Reviewer #2 (Public Review):

Weaknesses: 1. Although the current human ECoG data set is valuable, there is still large variability in electrode coverage across the patients (I fully acknowledge the difficulty). This makes statistical assessment a bit tricky. The potential factors of interest in the current study would be Electrode (=Region), Subject, Hemisphere, and their interactions. The tricky part is that Electrode is nested within Subject, and Subject is nested within Hemisphere. Permutation-based ANOVA used for the current paper requires proper treatment of these nested factors when making permutations (Anderson and Braak, 2003). With this regard, sufficient details about how the authors treated each factor, for instance, in each pbANOVA, are not provided in the current version of the manuscript. Similarly, the scope of statistical generalizability, whether the inference is within-sample or population-level, for the claims (e.g., statement about the hemispheric or regional difference) needs to be clarified.

We discuss at length the issue of electrode variability and have addressed this in the revised manuscript. Graphically, we have added a Supplemental Figure (S2). Statistically, we appreciate the point about the need for the analysis to address the nested structure of the data. We have redone all of the statistics, now using a permutation-based linear mixed effects model with a random effect of patient. This approach did not change any of the findings.

As to the comment about hemispheric or regional differences, the data show that both are important factors. Our hemispheric effect is characterized by stronger ipsilateral encoding in the left hemisphere and subsequently better across-arm generalization (Figures 2-4). We then examine the spatial distribution of electrodes that generalized well or poorly and found clusters in both hemispheres of electrodes that generalize poorly. In contrast, only in the left hemisphere did we find clusters of electrodes that generalize well. These electrodes were localized to PMd, PMv and superior parietal cortex (Fig 5D). In summary, we argue that activity patterns in M1 are similar in the left and right hemispheres, but there is a marked asymmetry for activity patterns over premotor and parietal cortices.

Additional contexts that would help readers interpret or understand the significance of the work: The greater amount of shared movement representation in the left hemisphere may imply the greater reliance of the left arm on the left hemisphere. This may, in turn, lead to the greater influence of the ongoing right arm motion on the left arm movement control during the bimanual coordination. Indeed, this point is addressed by the authors in the Discussion (page 15, lines 26-41). One critical piece of literature missing in this context is the work done by Yokoi, Hirashima, and Nozaki (2014). In the experiments using the bimanual reaching task, they in fact found that the learning by the left arm is to the greater degree influenced by the concurrent motion of the right arm than vice versa (Yokoi et al., J Neurosci, 2014). Together with Diedrichsen et al. (2013), this study will strengthen the authors' discussion and help readers interpret the present result of left hemisphere dominance in the context of more skillful bimanual action.

The Yokoi paper is a very important paper in revealing hemispheric asymmetries during skilled bimanual movements. However, we think it is problematic to link the hemispheric asymmetries we observe to the behavioral effects reported in the Yokoi paper (namely, that the nondominant, left arm was more strongly influenced by the kinematics of the right arm). One could hypothesize that the left hemisphere, given its representation of both arms, could be controlling both arms in some sort of direct way (and thus the action of the right arm will have an influence on left arm movement given the engagement of the same neural regions for both movements). It is also possible that the left hemisphere is receiving information about the state of both the right and left arms, and this underlies the behavioral asymmetry reported in Yokoi.

Reviewer #3 (Public Review):

In the present work, Merrick et al. analyzed ECoG recordings from patients performing out-and-back reaching movements. The authors trained a linear model to map kinematic features (e.g., hand speed, target position) to high frequency ECoG activity (HFA) of each electrode. The two primary findings were: 1) encoding strength (as assessed by held-out R2 values) of ipsilateral and contralateral movements was more bilateral in the left hemisphere than in the right and 2) across-arm generalization was stronger in the left hemisphere than in the right. As the authors point out in the Introduction, there are known 'asymmetries between the two hemispheres in terms of praxis', so it may not be surprising to find asymmetries in the kinematic encoding of the two hemispheres (i.e., the left hemisphere contributes 'more equally' to movements on either side of the body than the right hemisphere).

There is one point that I feel must be addressed before the present conclusions can be reached and a second clarification that I feel will greatly improve the interpretability of the results.

First, as is often the case when working with patients, the authors have no control over the recording sites. This led to some asymmetries in both the number of electrodes in each hemisphere (as the authors note in the Discussion) and (more importantly) in the location of the recording electrodes. Recording site within a hemisphere must be controlled for before any comparisons between the hemispheres can be made. For example, the authors note that 'the contralateral bias becomes weaker the further the electrodes are from putative motor cortex'. If there happen to be more electrodes placed further from M1 in the left hemisphere (as Supplementary Figure 1 seems to suggest), than we cannot know whether the results of Figures 2 and 3 are due to the left hemisphere having stronger bilateral encoding or simply more electrodes placed further from M1.

The reviewer makes a very valid point and this comment has led to our inclusion of a new Supplementary Figure, S2, in which we quantify the percentage of electrodes in each subregion.

Second, it would be useful if the authors provided a bit of clarification about what type of kinematic information the linear model is using to predict HFA. I believe the paragraph titled 'Target modulation and tuning similarity across arms' suggests that there is very little across-target variance in the HFA signal. Does this imply that the model is primarily ignoring the Phi and Theta (as well as their lagged counterparts) and is instead relying on the position and speed terms? How likely is it that the majority of the HFA activity around movement onset reflects a condition-invariant 'trigger signal' (Kaufman, et al., 2016). This trigger signal accounts for the largest portion of neural variance around movement onset (by far), and the weight of individual neurons in trigger signal dimensions tend to be positive, which means that this signal will be strongly reflected in population activity (as measured by ECoG). This interpretation does not detract from the present results in any way, but it may serve to clarify them.

To address this comment, we have added a new figure (Fig 6) which shows the relative contribution of each kinematic feature as well as their average weights across time for both contralateral and ipsilateral movements. This figure also addresses the reviewer’s question about the contribution of the target position to the model. As can be seen, features that reflect timing/movement initiation (position, speed) make a larger contribution compared to the two features which capture directional tuning (theta, phi). As the reviewer suggested, this result is in line Kaufman et al. (2016) which reported that a condition-invariant ‘trigger signal’ comprises the largest component of neural activity. We note that the target dependent features theta and phi still make a substantial contribution to the model (relative contribution: contra = 32%, ipsi = 37%). Previously, we have tested the contribution of the theta and phi features by comparing two models, one that only used position and speed (Movement model) and one that also included the two angular components phi and theta (Target Model). For a subset of electrodes, the held-out predictions were significantly better using the Target Model, a result we take as further evidence of electrode tuning within our dataset.

The figure below shows an electrode located in M1 that is tuned to targets when the patient reached with their contralateral arm as an example. We believe that having an explicit depiction of how the four features contribute to the HFA predictions will help the reader evaluate the model. These points are now addressed in the text in the results section discussing Figure 6.

Author Response

Reviewer #1 (Public Review):

[...] Recently, pupil dilation was linked to cholinergic and noradrenergic neuromodulation as well as cortical state dynamics in animal research. This work adds substantially to this growing research field by revealing the temporal and spatial dynamics of pupil-linked changes in cortical state in a large sample of human participants.

The analyses are thorough and well conducted, but some questions remain, especially concerning unbiased ways to account for the temporal lag between neural and pupil changes. Moreover, it should be stressed that the provided evidence is of indirect nature (i.e., resting state pupil dilation as proxy of neuromodulation, with multiple neuromodulatory systems influencing the measure), and the behavioral relevance of the findings cannot be shown in the current study.

Thank you for your positive feedback and constructive suggestions. We are especially grateful for the numerous pointers to other work relevant to our study.

1. Concerning the temporal lag: The authors' uniformly shift pupil data (but not pupil derivative) in time for their source-space analyses (see above). However, the evidence for the chosen temporal lags (930 ms and 0 ms) is not that firm. For instance, in the cited study by Reimer and colleagues [1] , cholinergic activation shows a temporal lag of ~ 0.5 s with regard to pupil dilation - and the authors would like to relate pupil time series primarily to acetylcholine. Moreover, Joshi and colleagues [2] demonstrated that locus coeruleus spikes precede changes in the first derivative of pupil dilation by about 300 ms (and not 0 ms). Finally, in a recent study recording intracranial EEG activity in humans [3], pupil dilation lagged behind neural events with a delay between ~0.5-1.7s. Together, this questions the chosen temporal lags.

More importantly, Figures 3 and S3 demonstrate variable lags for different frequency bands (also evident for the pupil derivative), which are disregarded in the current source-space analyses. This biases the subsequent analyses. For instance, Figure S3 B shows the strongest correlation effect (Z~5), a negative association between pupil and the alpha-beta band. However, this effect is not evident in the corresponding source analyses (Figure S5), presumably due to the chosen zero-time-lag (the negative association peaked at ~900 ms)).

As the conducted cross-correlations provided direct evidence for the lags for each frequency band, using these for subsequent analyses seems less biased.

This is an important point and we gladly take the opportunity to clarify this in detail. In essence, choosing one particular lag over others was a decision we took to address the multi-dimensional issue of presenting our results (spectral, spatial and time dimensions) and fix one parameter for the spatial description (see e.g. Figure 4). It is worth pointing out first that our analyses were all based on spectral decompositions that necessarily have limited temporal resolutions. Therefore, any given lag represents the center of a band that we can reasonably attribute to a time range. In fact, Figure 3C shows how spread out the effects are. It also shows that the peaks (troughs) of low and high frequency ranges align with our chosen lag quite well, while effects in the mid-frequency range are not “optimally” captured.

As picking lags based on maximum effects may be seen as double dipping, we note that we chose 0.93 sec a priori based on the existing literature, and most prominently based on the canonical impulse response of the pupil to arousing stimuli that is known to peak at that latency on average (Hoeks & Levelt, 1993; Wierda et al. 2012; also see Burlingham et al.; 2021). This lag further agrees with the results of reference [3] cited by the reviewer as it falls within that time range, and with Reimer et al.’s finding (cited as [1] above), as well as Breton-Provencher et al. (2019) who report a lag of ~900 ms sec (see their Supplementary Figure S8) between noradrenergic LC activation and pupil dilation. Finally, note that it was not our aim to relate pupil dilations to either ACh or NE in particular as we cannot make this distinction based on our data alone. Instead, we point out and discuss the similarities of our findings with time lags that have been reported for either neurotransmitter before.

With respect to using different lags, changing the lag to 0 or 500 msec is unlikely to alter the reported effects qualitatively for low- and high frequency ranges (see Figure 3C), as both the pupil time series as well as fluctuations in power are dominated by very slow fluctuations (<< 1 Hz). As a consequence, shifting the signal by 500 msec has very little impact. For comparison, below we provide the reviewer with the results presented in Figure 4 but computed based on zero (Figure R1) and 500-msec (Figure R2) lags. While there are small quantitative differences, qualitatively the results remain mostly identical irrespective of the chosen lag.

Figure R1. Figure equivalent to main Figure 4, but without shifting the pupil.

In sum, choosing one common lag a priori (as we did here) does not necessarily impose more of a bias on the presentation of the results than choosing them post-hoc based on the peaks in the cross-correlograms. However, we have taken this point as a motivation to revise the Results and Methods sections where applicable to strengthen the rationale behind our choice. Most importantly, we changed the first paragraph that mentions and justifies the shift as follows, because original wording may have given the false impression that the cross-correlation results influenced lag choice:

“Based on previous reports (Hoeks & Levelt, 1993; Joshi et al., 2016; Reimer et al., 2016), we shifted the pupil signal 930 ms forward (with respect to the MEG signal). We introduced this shift to compensate for the lag that had previously been observed between external manipulations of arousal (Hoeks & Levelt, 1993) as well as spontaneous noradrenergic activity (Reimer et al., 2016) and changes in pupil diameter. In our data, this shift also aligned with the lags for low- and high-frequency extrema in the cross-correlation analysis (Figure 3B).”

Figure R2. Figure equivalent to main Figure 4, but with shifting the pupil with respect to the MEG by 500 ms.

Related to this aspect: For some parts of the analyses, the pupil time series was shifted with regard to the MEG data (e.g., Figure 4). However, for subsequent analyses pupil and MEG data were analyzed in concurrent 2 s time windows (e.g., Figure 5 and 6), without a preceding shift in time. This complicates comparisons of the results across analyses and the reasoning behind this should be discussed.

The signal has been shifted for all analyses that relate to pupil diameter (but not pupil derivative). We have added versions of the following statement in the respective Results and Methods section to clarify (example from Results section ‘Nonlinear relations between pupil-linked arousal and band-limited cortical activity’):

“In keeping with previous analyses, we shifted the pupil time series forward by 930 msec, while applying no shift to the pupil derivative.”

1. The authors refer to simultaneous fMRI-pupil studies in their background section. However, throughout the manuscript, they do not mention recent work linking (task-related) changes in pupil dilation and neural oscillations (e.g., [4-6]) which does seem relevant here, too. This seems especially warranted, as these findings in part appear to disagree with the here-reported observations. For instance, these studies consistently show negative pupil-alpha associations (while the authors mostly show positive associations). Moreover, one of these studies tested for links between pupil dilation and aperiodic EEG activity but did not find a reliable association (again conflicting with the here-reported data). Discussing potential differences between studies could strengthen the manuscript.

We have added a discussion of the suggested works to our Discussion section. We point out however that a recent study (Podvalny et al., https://doi.org/10.7554/eLife.68265) corroborates our finding while measuring resting-state pupil and MEG simultaneously in a situation very similar to ours. Also, we note that Whitmarsh et al. (2021) (reference [6]) is actually in line with our findings as we find a similar negative relationship between alpha-range activity in somatomotor cortices and pupil size.

Please also take into account that results from studies of task- or event-related changes in pupil diameter (phasic responses) cannot be straightforwardly compared with the findings reported here (focusing on fluctuations in tonic pupil size) , due to the inverse relationship between tonic (or baseline) and phasic pupil response (e.g. Knapen et al., 2016). This means that on trials with larger baseline pupil diameter, phasic pupil dilation will be smaller and vice versa. Hence, a negative relation between the evoked change in pupil diameter and alpha-band power can very well be consistent with the positive correlation between tonic pupil diameter and alpha-band activity that we report here for visual cortex.

In section ‘Arousal modulates cortical activity across space, time and frequencies’ we have added:

“Seemingly contradicting the present findings, previous work on task-related EEG and MEG dynamics reported a negative relationship between pupil-linked arousal and alpha-range activity in occipito-parietal sensors during visual processing (Meindertsma et al, 2017) and fear conditioning (Dahl et al. 2020).Note however that results from task-related experiments, that focus on evoked changes in pupil diameter rather than fluctuations in tonic pupil size, cannot be directly compared with our findings. Similar to noradrenergic neurons in locus coeruleus (Aston-Jones & Cohen, 2005), phasic pupil responses exhibit an inverse relationship with tonic pupil size (Knapen et al., 2016). This means that on trials with larger baseline pupil diameter (e.g. during a pre-stimulus period), the evoked (phasic) pupil response will be smaller and vice versa. As a consequence, a negative correlation between alpha-band activity in the visual cortex and task-related phasic pupil responses does not preclude a positive correlation with tonic pupil size during baseline or rest as reported here. In line with this, Whitmarsh et al., 2021 found a negative relationship between alpha-activity and pupil size in the somatosensory cortex that agrees with our finding. Although using an event-related design to study attention to tactile stimuli, this relationship occurred in the baseline, i.e. before observing any task-related phasic effects on pupil-linked arousal or cortical activity.”

In section ‘Arousal modulation of cortical excitation-inhibition ratio’ we have added: “The absence of this effect in visual cortices may explain why Kosciessa et al. (2021) found no relationship between pupil-linked arousal and spectral slope when investigating phasic pupil dilation in response to a stimulus during visual task performance. However, this behavioral context, associated with different arousal levels, likely also changes E/I in the visual cortex when compared with the resting state (Pfeffer et al., 2018).”

Finally, in the Conclusion we added (note: ‘they’ = the present results): “Further, they largely agree with similar findings of a recent independent report (Podvalny et al., 2021).”

Related to this aspect: The authors frequently relate their findings to recent work in rodents. For this it would be good to consider species differences when comparing frequency bands across rodents and primates (cf. [7,8]).

Throughout our Results section we have mainly remained agnostic with respect to labeling frequency ranges when drawing between-species comparisons, and have only reverted to it as a justification for a dimension reduction for some of the presented analysis. Following your comment however, we have phrased the following section in the Discussion, section ‘Arousal modulates cortical activity across space, time and frequencies’, more carefully:

“The low-frequency regime referred to in rodent work (2—10Hz; e.g., McGinley et al., 2015) includes activity that shares characteristics with human alpha rhythms (3—6Hz; Nestogel and McCormick, 2021; Senzai et al. 2019). The human equivalent however clearly separates from activity in lower frequency bands and,here, showed idiosyncratic relationships with pupil-linked arousal.”

1. Figure 1 highlights direct neuromodulatory effects in the cortex. However, seminal [9-11] and more recent work [12,13] demonstrates that noradrenaline and acetylcholine also act in the thalamus which seems relevant concerning the interpretation of low frequency effects observed here. Moreover, neural oscillations also influence neuromodulatory activity, thus the one-headed arrows do not seem warranted (panel C) [3,14].

This is a very good point. First, we would like to note that we have extended on acknowledging thalamic contributions to low-frequency (specifically alpha) effects in response to the Reviewer’s point 11 (‘Recommendations for authors’ section below). Also, we have added a reference to the role of potential top-down (reverse) influences to our Discussion, section ‘Arousal modulates cortical activity across space, time and frequencies’, as follows:

“Further, we note that our analyses and interpretations focus on arousal-related neuromodulatory influences on cortical activity, whereas recent work also supports a reverse “top-down” route, at least for frontal cortex high-frequency activity on LC spiking activity (Totah et al., 2021).”

Ultimately, however, we decided to leave the arrows in Figure 1C uni-directional to keep in line with the rationale of our research that stems mostly from rodent work, which also emphasises the indicated directionality. Also, reference [3] is highly interesting for us because it actually aligns with our data: The authors show that a spontaneous peak of high-frequency band activity (>70 Hz) in insular cortex precedes a pupil dilation peak (or plateau) in two of three participants by ~500msec (which mimics a pattern found for task-evoked activity; see their Figure 5b/c). We find a maximum in our cross-correlation between pupil size and high frequency band activity (>64 Hz) that indicates a similar lag (see our Figure 3B). Importantly, both results do not rule out a common source of neuromodulation for the effects. We have added the following to the end of the section ‘An arousal-triggered cascade of activity in the resting human brain’:

“In fact, Kucyi & Parvizi (2020) found spontaneous peaks of high-frequency band activity (>70 Hz) in the insular cortex of three resting surgically implanted patients that preceded pupil dilation by ~500msec - a time range that is consistent with the lag of our cross-correlation between pupil size and high frequency (>64Hz) activity (see Figure 3B). Importantly, they showed that this sequence mimicked a similar but more pronounced pattern during task performance. Given the purported role of the insula (Menon & Uddin, 2015), this finding lends support to the idea that spontaneous covariations of pupil size and cortical activity signal arousal events related to intermittent 'monitoring sweeps' for behaviourally relevant information.”

1. In their discussion, the authors propose a pupil-linked temporal cascade of cognitive processes and accompanying power changes. This argument could be strengthened by showing that earlier events in the cascade can predict subsequent ones (e.g., are the earlier low and high frequency effects predictive of the subsequent alpha-beta synchronization?)-

We added this cascade angle as one possible interpretation of the observed effects. We fully agree that this is an interesting question but would argue that this would ideally be tested in follow-up research specifically designed for that purpose. The suggested analysis would add a post-hoc aspect to our exploratory investigation in the absence of a suitable contrast, while also potentially side-tracking the main aim of the study. We have revised the language in this section and added the following changes (bold) to the last paragraph to emphasise the speculatory aspect, and clarify what we think needs to be done to look into this further and with more explanatory power.

“The three scenarios described here are not mutually exclusive and may explain one and the same phenomenon from different perspectives. Further, it remains possible that the sequence we observe comprises independent effects with specific timings. A pivotal manipulation to test these assumptions will be to contrast the observed sequence with other potential coupling patterns between pupil-linked arousal and cortical activity during different behavioural states.”

Author Response

Reviewer #1 (Public Review):

This thorough study expands our understanding of BMP signaling, a conserved developmental pathway, involved in processes diverse such as body patterning and neurogenesis. The authors applied multiple, state-of-art strategies to the anthozoan Nematostella vectensis in order to first identify the direct BMP signaling targets - bound by the activated pSMAD1/5 protein - and then dissect the role of a novel pSMAD1/5 gradient modulator, zwim4-6. The list of target genes features multiple developmental regulators, many of which are bilaterally expressed, and which are notably shared between Drosophila and Xenopus. The analysis identified in particular zswim4-6 a novel nuclear modulator of the BMP pathway conserved also in vertebrates. A combination of both loss-of-function (injection of antisense morpholino oligonucleotide, CRISPR/Cas9 knockout, expression of dominant negative) and gain-of-function assays, and of transcriptome sequencing identified that zwim acts as a transcriptional repression of BMP signaling. Functional manipulation of zswim5 in zebrafish shows a conserved role in modulating BMP signaling in a vertebrate.

The particular strength of the study lies in the careful and thorough analysis performed. This is solid developmental work, where one clear biological question is progressively dissected, with the most appropriate tools. The functional results are further validated by alternative approaches. Data is clearly presented and methods are detailed. I have a couple of comments.

1) I was intrigued - as the authors - by the fact that the ChiP-Seq did not identify any known BMP ligand bound by pSMAD1/5. Are these genes found in the published ChiP-Seq data of the other species used for the comparative analysis? One hypothesis could be that there is a change in the regulatory interactions and that the initial set-up of the gradient requires indeed a feedback loop, which is then turned off at later gastrula. In this case, immunoprecipitation at early gastrula, prior to the set-up of the pSMAD1/5 gradient, could reveal a different scenario. Alternately, the regulation could be indirect, for example, through RGM, an additional regulator of BMP signaling expressed on the side of lower BMP activity, which is among the targets of the ChiP-Seq. This aspect could be discussed. Additionally, even if this is perhaps outside the scope of this study, I think it would be informative to further assess the effect of ZSWIM manipulation on RGM (and vice versa).

Indeed, BMP genes are direct BMP signaling targets in Drosophila (dpp) (Deignan et al., 2016, https://doi.org/10.1371/journal.pgen.1006164) and frog (bmp2, bmp4, bmp5, bmp7) (Stevens et al., 2021, https://doi.org/10.1242/dev.145789). Of all these ligands, only the dorsally expressed Xenopus bmp2 is repressed by BMP signaling, while another dorsally expressed Xenopus BMP gene admp is not among the direct targets. All other BMP genes listed here are expressed in the pMad/pSMAD1/5/8-positive domain and are activated by BMP signaling.

In Nematostella, we do not find BMP genes among the ChIP-Seq targets, but this is not that surprising considering the dynamics of the bmp2/4, bmp5-8 and chordin expression, as well as the location of the pSMAD1/5-positive cells. In late gastrulae/early planulae, Chordin appears to be shuttling BMP2/4 and BMP5-8 away from their production source and over to the gdf5-like side of the directive axis (Genikhovich et al., 2015; Leclere and Rentsch, 2014). By 4 dpf, chordin expression stops, and BMP2/4 and BMP5-8 start to be both expressed AND signal in the mesenteries. If bmp2/4 and bmp5-8 expression were directly suppressed by pSMAD1/5 (as is the case chordin or rgm expression), this mesenterial expression would not be possible. Therefore, in our opinion, it is most likely that at late gastrula and early planula the regulation of bmp2/4 and bmp5-8 expression by BMP signaling is indirect. We do not have an explanation for why gdf5-like (another BMP gene expressed on the “high pSMAD1/5” side) is not retrieved as a direct BMP target in our ChIP data. Since we do not understand well enough how BMP gene expression is regulated, we do not discuss this at length in the manuscript.

As the Reviewer suggested, we analyzed the effect of ZSWIM4-6 KD on the expression of rgm. Expectedly, since it is expressed on the “low BMP side”, its expression was strongly expanded (Figure 6 - Figure Supplement 4)

2) I do not fully understand the rationale behind the choice of performing the comparative assays in zebrafish: as the conservation was initially identified in Xenopus, I would have expected the experiment to be performed in frog. Furthermore, reading the phylogeny (Figure 4A), it is not obvious to me why ZSWIM5 was chosen for the assay (over the other paralog ZSWIM6). Could the Authors comment on this experiment further?

The comparison was done in zebrafish because we were planning to generate zswim5 mutants, whose analysis is currently in progress. ZSWIM6 is not expressed at the developmental stages we were interested in, while ZSWIM5 was, based on available zebrafish expression data (White et al., 2017):

Reviewer #2 (Public Review):

The authors provide a nice resource of putative direct BMP target genes in Nematostella vectensis by performing ChIP-seq with an anti-pSmad1/5 antibody, while also performing bulk RNA-seq with BMP2/4 or GDF5 knockdown embryos. Genes that exhibit pSmad1/5 binding and have changes in transcription levels after BMP signaling loss were further annotated to identify those with conserved BMP response elements (BREs). Further characterization of one of the direct BMP target genes (zswim4-6) was performed by examining how expression changed following BMP receptor or ligand loss of function, as well as how loss or gain of function of zswim4-6 affected development and BMP signaling. The authors concluded that zswim4-6 modulates BMP signaling activity and likely acts as a pSMAD1/5 dependent co-repressor. However, the mechanism by which zswim4-6 affects the BMP gradient or interacts with pSMAD1/5 to repress target genes is not clear. The authors test the activity of a zswim4-6 homologue in zebrafish (zswim5) by over-expressing mRNA and find that pSMAD1/5/9 labeling is reduced and that embryos have a phenotype suggesting loss of BMP signaling, and conclude that zswim4-6 is a conserved regulator of BMP signaling. This conclusion needs further support to confirm BMP loss of function phenotypes in zswim5 over-expression embryos.

Major comments

1) The BMP direct target comparison was performed between Nematostella, Drosophila, and Xenopus, but not with existing data from zebrafish (Greenfeld 2021, Plos Biol). Given the functional analysis with zebrafish later in the paper it would be nice to see if there are conserved direct target genes in zebrafish, and in particular, is zswim5 (or other zswim genes) are direct targets. Since conservation of zswim4-6 as a direct BMP target between Nematostella and Xenopus seemed to be part of the rationale for further functional analysis, it would also be nice to know if this is a conserved target in zebrafish.

Thank you for the suggestion. In the paper by Greenfeld et al., 2021, zebrafish zswim5 was downregulated approximately 2.4x in the bmp7 mutant at 6 hpf, while zswim6 was barely expressed and not affected at this stage. We added this information to the text of the manuscript. Expression of several other zebrafish zswim genes was also affected in the bmp7 mutant, but these genes do not appear relevant for our study since their corresponding orthologs are not identified as pSMAD1/5 ChIP-Seq targets in Nematostella. Notably, zebrafish zzswim5 is not clearly differentially expressed in BMP or Chd overexpression conditions (See Supplementary file 1 in Rogers et al. 2020). Importantly, in the paper, we wanted to compare ChiP-Seq data with ChIP-Seq data, however, unfortunately, no ChIP-Seq data for pSMAD1/5/8 is currently available for zebrafish, thus precluding comparisons.

Related to this, in the discussion it is mentioned that zswim4/6 is also a direct BMP target in mouse hair follicle cells, but it wasn't obvious from looking at the supplemental data in that paper where this was drawn from.

Please see Supplementary Table 1, second Excel sheet labeled “Mx ChIP_Seq” in Genander et al., 2014, https://doi.org/10.1016/j.stem.2014.09.009. Zswim4 has a single pSMAD1 peak associated with it, Zswim6 has two.

2) The loss of zswim4-6 function via MO injection results in changes to pSmad1/5 staining, including a reduction in intensity in the endoderm and gain of intensity in the ectoderm, while over-expression results in a loss of intensity in the ectoderm and no apparent change in the endoderm. While this is interesting, it is not clear how zswim4-6 is functioning to modify BMP signaling, and how this might explain differential effects in ectoderm vs. endoderm. Is the assumption that the mechanism involves repression of chordin? And if so one could test the double knockdown of zswim4-6 and chordin and look for the rescue of pSad1/5 levels or morphological phenotype.

We do not think that the mechanism of the ZSWIM4-6 action is via repression of Chordin. As loss of chordin leads to the loss of pSMAD1/5 in Nematostella (Genikhovich et al., 2015), the proposed experiment is, unfortunately, not feasible to test this hypothesis. Currently, we see two distinct effects of the modulation of zswim4-6 expression. First, it affects the pSMAD1/5 gradient, possibly by destabilizing nuclear SMAD1/5, as has been proposed by Wang et al., 2022 for the vertebrate Zswim4. This is in line with our results shown on Fig. 6C-F’ and Fig. 6-Figure supplement 3. In our opinion, the reaction of the genes expressed on the “high BMP” side of the directive axis to the overexpression or KD of ZSWIM4-6 (Fig. 6I-K’, 6N-P’) can be explained by these changes in the pSMAD1/5 signaling intensity. Secondly, zswim4-6 appears to promote pSMAD1/5-mediated gene repression. This is in line with the reaction of the genes expressed on the “low BMP” side of the directive axis (Fig. 6G-H’, 6L-M’, Fig. 6-Figure Supplement 4). These genes are repressed by BMP signaling, but they expand their expression upon zswim4-6 KD in spite of the increased pSMAD1/5. Our ChiP experiment (Fig. 6Q) supports this view.

3) Several experiments are done to determine how zswim4-6 expression responds to the loss of function of different BMP ligands and receptors, with the conclusion being that swim4-6 is a BMP2/4 target but not a GDF5 target, with a lot of the discussion dedicated to this as well. However, the authors show a binary response to the loss of BMP2/4 function, where zswim4-6 is expressed normally until pSmad1/5 levels drop low enough, at which point expression is lost. Since the authors also show that GDF5 morphants do not have as strong a reduction in pSmad1/5 levels compared to BMP2/4 morphants, perhaps GDF5 plays a positive but redundant role in swim4-6 expression. To test this possibility the authors could inject suboptimal doses of BMP2/4 MO with GDF5 MO and look for synergy in the loss of zswim4-6 expression.

Thanks for this great suggestion! We performed this experiment (Fig. 5H’’-L) and indeed, a suboptimal dose of BMP2/4MO + GDF5lMO results in a complete radialization of the embryo and abolished zswim4–6, similar to the effect of a high dose of BMP2/4. This result suggests that rather than being a ligand-specific signaling function, GDF5-like signaling alone still provides sufficiently high pSmad1/5 levels to activate zswim4-6 expression to apparent wildtype levels, demonstrating the sensitivity of this gene to even very low amounts of BMP signaling.

4) The zswim4-6 morphant embryos show increased expression of zswim4-6 mRNA, which is said to indicate that zswim4-6 negatively regulates its own expression. However in zebrafish translation blocking MOs can sometimes stabilize target transcripts, causing an artifact that can be mistakenly assumed to be increased transcription (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7162184/). Some additional controls here would be warranted for making this conclusion.

Thanks for raising this important experimental consideration. To-date, we do not have any evidence for MO-mediated transcript stabilization in Nematostella, and we have not found such data in the literature on models other than zebrafish. mRNA stabilization by the MO also seemed unlikely because we were unable to KD zswim4-6 using several independent shRNAs - an effect we frequently observe with genes, whose activity negatively regulates their own expression. However, to test the possibility that zswim4-6MO binding stabilizes zswim4-6 mRNA, we injected mRNA containing the zswim4-6MO recognition sequence followed by the mCherry coding sequence (zswim4-6MO-mCherrry) with either zswim4-6MO or control MO. We could clearly detect mCherry fluorescence at 1 dpf if control MO was co-injected with the mRNA, but not if zswim4-6MO was coninjected with the mRNA. At 2 dpf (the stage at which we showed upregulation of zswim4-6 upon zswim4-6MO injection on Fig. 6I-I’), zswim4-6MO-mCherrry mRNA was undetectable by in situ hybridization with our standard FITC-labeled mCherry probe independent of whether zswim4-6MO-mCherrry mRNA was co-injected with the control MO or ZSWIM4-6MO, while hybridization with the FITC-labeled FoxA probe worked perfectly.

Author response image 1.

We are currently offering two alternative hypothesis for the observed increase in zswim4-6 levels in the paper rather than stating explicitly that ZSWIM4-6 negatively regulates its own expression: “The KD of zswim4-6 translation resulted in a strong upregulation of zswim4-6 transcription, especially in the ectoderm, suggesting that ZSWIM4-6 might either act as its own transcriptional repressor or that zswim4-6 transcription reacts to the increased ectodermal pSMAD1/5 (Fig. 6I-I’).” Given the sensitivity of zswim4-6 to even the weakest pSMAD1/5 signal (zswim4/6 is expressed upon GDF5-like KD, which drastically reduces pSMAD1/5 signaling intensity (see Fig. 1 and 2 in Genikhovich et al., 2015, http://doi.org/10.1016/j.celrep.2015.02.035 and Fig. 6-Figure supplement 3 of this paper), the latter option (that it reacts to the increased ectodermal pSMAD1/5) is, in our opinion, clearly the more probable one.

5) Zswim4-6 is proposed to be a co-repressor of pSmad1/5 targets based on the occupancy of zswim4-6 at the chordin BRE (which is normally repressed by BMP signaling) and lack of occupancy at the gremlin BRE (normally activated by BMP signaling). This is a promising preliminary result but is based only on the analysis of two genes. Since the authors identified BREs in other direct target genes, examining more genes would better support the model.

We suggest that ZSWIM4-6 may be a co-repressor of pSMAD1/5 targets because it is a nuclear protein (Fig. 4G), whose knockdown results in the expansion of the ectodermal expression of several genes repressed by pSMAD1/5 in spite of the expansion of pSMAD1/5 itself (Fig. 6G-H’, 6L-M’, Fig. 6-Figure Supplement 4). Our limited ChIP analysis supports this idea by showing that ZSWIM4-6 is bound to the pSMAD1/5 site of chordin (repressed by pSMAD1/5) but not on gremlin (activated by pSMAD1/5). We agree that adding the analysis of more targets in order to challenge our hypothesis would be good. However, given technical limitations (having to inject many thousands of eggs with the EF1a::ZSWIM4-6-GFP plasmid in order to get enough nuclei to extract sufficient immunoprecipitated chromatin for qPCR on 3 genes (chordin, gremlin, GAPDH) for each biological replicate, it is currently unfortunately not feasible to test more genes. It will be of great interest for follow up studies to generate a knock-in line with tagged zswim4-6 to analyze target binding on a genome-wide scale. We stress in the discussion that currently the power of our conclusion is low.

6) The rationale for further examination of zswim4-6 function in Nematostella was based in part on it being a conserved direct BMP target in Nematostella and Xenopus. The analysis of zebrafish zswim5 function however does not examine whether zswim5 is a BMP target gene (direct or indirect). BMP inhibition followed by an in situ hybridization for zswim5 would establish whether its expression is activated downstream of BMP.

In the paper by Greenfeld et al., 2021, zebrafish zswim5 was downregulated approximately 2.4x in the bmp7 mutant at 6 hpf. However, this gene was not among the 57 genes, which were considered to be direct BMP targets because their expression was affected by bmp7 mRNA injection into cycloheximide-treated bmp7 mutants (Greenfeld et al., 2021). We added this information to the text of the manuscript.

7) Although there is a reduction in pSmad1/5/9 staining in zebrafish injected with zswim5 mRNA, it is difficult to tell whether the resulting morphological phenotypes closely resemble zebrafish with BMP pathway mutations (such as bmp2b). More analysis is warranted here to determine whether stereotypical BMP loss of function phenotypes are observed, such as dorsalization of the mesoderm and loss of ventral tail fin.

We agree, and we have tuned down all zebrafish arguments. Analyses of zswim5 mutants are currently ongoing.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors investigate the genes involved in the retention of eggs in Aedes aegypti females. They do so by identifying two candidate genes that are differentially expressed across the different reproductive phases and also show that the transcripts of those two genes are present in ovaries and in the proteome. Overall, I think this is interesting and impressive work that characterizes the function of those two specific protein-coding genes thoroughly. I also really enjoyed the figures. Although they were a bit packed, the visuals made it easy to follow the authors' arguments. I have a few concerns and suggested changes, listed below.

1) These two genes/loci are definitely rapidly evolving. However, that does not automatically imply that positive selection has occurred in these genes. Clearly, you have demonstrated that these gene sequences might be important for fitness in Aedes aegypti. However, if these happen to be disordered proteins, then they would evolve rapidly, i.e., under fewer sequence constraints. In such a scenario, dN/dS values are likely to be high. Another possibility is that as these are expressed only in one tissue and most likely not expressed constitutively, they could be under relaxed constraints relative to all other genes in the genome. For instance, we know that average expression levels of protein-coding genes are highly correlated with their rate of molecular evolution (Drummond et al., 2005). Moreover, there have clearly been genome rearrangements and/or insertion/deletions in the studied gene sequences between closely- related species (as you have nicely shown), thus again dN/dS values will naturally be high. Thus, high values of dN/dS are neither surprising nor do they directly imply positive selection in this case. If the authors really want to investigate this further, they can use the McDonald Kreitman test (McDonald and Kreitman 1991) to ask if non- synonymous divergence is higher than expected. However, this test would require population-level data. Alternatively, the authors can simply discuss adaptation as a possibility along with the others suggested above. A discussion of alternative hypotheses is extremely important and must be clearly laid out.

We agree with the reviewer’s point that rapid evolution is not the same as positive selection. We also agree with the reviewer’s point that McDonald-Kreitman test (MK test) is more powerful than dN/dS analysis. We took advantage of a large population dataset from Rose et al. 2020. After filtering the data, we kept 454 genomes for MK tests. We found both genes are marginally significant or insignificant (tweedledee p = 0.068; tweedledum p = 0.048), despite that these are small genes and have low Pn values. This suggests that it is likely the genes evolve under positive selection.

In line with the reviewer’s suggestion, we performed another analysis using a large amount of population data. We asked if the SNP frequencies of tweedledee and tweedledum are correlated with environmental variables. We found that when compared to a distribution of 10,000 simulated genes with randomly-sampled genetic variants, both tweedledee and tweedledum showed significant correlation to multiple ecological variables reflecting climate variability, such as mean diurnal range, temperature seasonality, and precipitation seasonality (p<0.05). These results are now incorporated into the manuscript in Figure 5 and Figure 5 – Figure supplement 1.

2) The authors show that the two genes under study are important for the retention of viable eggs. However, as these genes are close to two other conserved genes (scratch and peritrophin-like gene), it is unclear to me how it is possible to rule out the contribution of the conserved genes to the same phenotype. Is it possible that the CRISPR deletion leads to the disruption of expression of one of the other important genes nearby (i.e., in a scratch or peritrophin-like gene) as the deleted region could have included a promoter region for instance, which is causing the phenotype you observe? Since all of these genes are so close to each other, it is possible that they are co-regulated and that tweedledee and tweedledum and expressed and translated along with the scratch and peritrophin-like gene. Do we know whether their expression patterns diverge and that scratch and peritrophin-like genes do not play a role in the retention of viable eggs?

This is a fair criticism; however, we think the chance that the phenotypes are caused by interrupting nearby genes is very low. First, peritrophin-like acts in the immune response, and scratch is a brain-biased transcription factor. Neither of the genes show expression in the ovary before or after blood feeding (TPM <1 or 2 are generally considered unexpressed, while scratch and peritrophin-like expression levels are overall lower than 0.1 TPM).

This suggests that peritrophin-like and scratch are not likely to function in the ovary. Thus, although we cannot completely rule out the gene knockout impacts regulation of very distant genes, it is unlikely. Since the mounting evidence we show in this manuscript that tweedledee and tweedledum are highly translated in the ovary after blooding feeding, under the principle of parsimony, we expect the phenotypes came from knocking out the highly expressed and translated genes.

Reviewer #2 (Public Review):

This manuscript is overall quite convincing, presenting a well- thought-out approach to candidate gene detection and systemic follow- ups on two genes that meet their candidate gene criteria. There are several major claims made by the authors, and some have more compelling evidence than others, but in general, the conclusions are quite sound. My main issues stem from how the strategy to identify genes playing a role in egg retention success has led to very particular genes being examined, and so I question some of the elements of the discussion focusing on the rapid evolution and taxon- uniqueness of the identified genes. In short, while I believe the authors have demonstrated that tweedledee and tweedledum play an important role in egg retention, I'm not sure whether this study should be taken as evidence that taxon-specific or rapidly evolving genes, in general, are responsible for this adaptation, or simply play an important role in it.

We have revised the paper to make it clearer that the focus is indeed on these two genes on not on the greater question of taxon-specific or rapidly-evolving genes.

First, the authors present evidence that Aedes aegypti females can retain eggs when a source of fresh water is lacking, confirming that females are not attracted to human forearms while retaining eggs and that up to 70% of the retained eggs hatch after retaining them for nearly a week. This ability is likely an important adaptation that allows Aedes aegypti to thrive in a broad range of conditions. The data here seem fairly compelling.

Based on this observation, the authors reason that genes responsible for the ability to retain eggs must: 1) be highly expressed in ovaries during retention, but not before or after. 2) be taxon-specific (as this behavior seems limited to Aedes aegypti). While this approach to enriching candidate genes has proven fruitful in this particular case, I'm not sure I agree with the authors' rationale. First, even genes at a low expression in the ovaries may be crucial to egg retention. Second, while egg-laying behavior is vastly varied in insects, I'm not sure focusing on taxon-restricted genes is necessary. It is entirely possible that many of the genes identified in Figure 2E play a crucial role in egg retention evolution. These are minor issues, but they are relevant to some later points made by the authors.

We regret framing the discovery of tweedledee and tweedledum in the original submission using this somewhat artificial set of filtering criteria. The reality is that the genes caught our attention for their novel sequence, tight genetic linkage, and interesting expression profile. That really is the focus of the paper, not these other peripheral questions that have been the focus of attention of the reviews. We really do apologize for all of the confusion about what this paper is about.

Nonetheless, the authors provide very compelling evidence that the two genes meeting their criteria - tweedledee and tweedledum, play an important role in egg retention. The genes seem to be expressed primarily in ovaries during egg retention (some observed expression in brain/testes is expected for any gene), and the proteins they code seem to be found in elevated quantities in both ovaries and hemolymph during and immediately after egg retention. RNA for the genes is detected in follicles within the ovary, and CRISPR knockouts of both the genes lead to a large decrease in egg viability post retention.

My earlier qualms about their search strategy relay into some issues with Figure 4, which describes how the two genes are 1) taxon- restricted and 2) have evolved very rapidly. Neither of the two statements is unexpected given the authors' search strategy. Of course, the genes examined precisely for their lack of homologs do not have any homologs. Similarly, by limiting themselves to genes that show a lack of homology (i.e. low sequence similarity) to other genes as well as genes with high expression levels in the ovaries, a higher rate of evolution is almost inevitable to infer (as ovary expressed genes tend to evolve more rapidly in mosquitoes). I agree with the authors that inferences of the evolutionary history of these genes are quite difficult because of their uniqueness, and I especially appreciate their attempts to identify homologs (although I really dislike the term "conceptualog").

We have removed our term “conceptualog” and replaced with the mor conventional “putative ortholog”

This leads to my main (fairly minor) issue of the paper - the discussion on the evolutionary history of these genes and its implications (sections "Taxon-restricted genes underlie tailored adaptations in a diverse world" and "Evolutionary histories and catering to different natural histories"). As noted, inferring this history is very difficult because the authors have focused on two rapidly evolving, taxon-restricted genes. The analyses they have performed here definitely demonstrate that the genes play an important role in egg retention, however, they do not show that taxon-restricted genes play a disproportionate role in egg retention evolution. Indeed, the only data relevant to this point would be the proportion of genes in Figure 2E that are taxon-restricted (3/9), but I'm not sure what the null expectation for this proportion for highly expressed ovary genes is to begin with. Furthermore, the extremely rapid evolution of this gene makes it hard to judge how truly taxon-restricted it is. My own search of tweedle homologs identified multiple as previously having been predicted to be "Knr4/Smi1-like", and while no similar genes are located in a similar location in melanogaster, there is generally little synteny conservation in Drosophila (for instance Bhutkar et al 2008), so I'm unsure what can really be said about their evolutionary origins/lack of homologs in Drosophila.

In short - the manuscript makes clear that tweedledee and tweedledum play an important role in egg retention in A. aegypti, nonetheless, it is not clear that this is a demonstration of how important taxon- restricted genes are to understanding the evolution of life-history strategies.

Again, we should have never framed the paper the way we did in the original version. We make no claims whatsoever that taxon-restricted genes in general should play a role in this biology, only that the two candidate genes under study influence egg viability after extended retention. We hope that the framing is clearer in this revision.

Author Response:

Reviewer #1 (Public Review):

This study sought to systematically identify the components and driving forces of transcriptome evolution in fungi that exhibit complex multicellularity (CM). The authors examined a series of parameters or expression signatures (i.e. natural antisense transcripts, allele-specific expression, RNA-editing) concluding that the best predictor of a gene behavior in the CM transcriptome was evolutionary age.

Thus, the transcriptomes of fruiting bodies showed a distinct gene-age-related stratification, where it was possible to sort out genes related to general sexual processes from those likely linked to morphogenetic aspects of the CM fruiting bodies. Notably, their results did not support a developmental hourglass, which is the rather predominant hypothesis in metazoans, including some analysis in fungi.

The studies involved analyses of new transcriptomic datasets for different developmental stages (and tissue types in some cases) of Pleurotus ostreatus and Pterula gracilis, as well as the analyses of existing datasets for other fungi.

There are diverse interesting observations such as ones regarding Allele Specific Expression (ASE), suggesting that in P. ostreatus ASE mainly occurs due to cis-regulatory allele divergence, possibly in fast evolving genes that are not under strong selection constraints, such as ones grouped in youngest gene ages categories. In addition, a large number of conserved unannotated genes among CM-specific orthogroups highlights the rather cryptic nature of CM in fungi and raises as an important area for future research.

Some of the key aspects of the analyses would need to be better exemplified such as:

– Providing a better description of the developmentally expressed TFs only in CM species

– Providing clear examples of the promoter divergence that could be the underlying mechanism behind ASE. In particular, for some cases, there may be enough information in the literature/databases to predict the appearance or disappearance of relevant cis-elements in the promoters showing the highest divergence in genes depicting the highest levels of ASE.

We appreciate the constructive comments of the Reviewer and have revised the ms in accordance with the suggestions. In particular, we link different parts of the ms better to each other, provided a more detailed discussion of developmentally expressed TFs (lines 615-621). We also provide case studies of ASE genes with cis-regulatory divergence (Figure 5 and see below), although we note that these analyses are based on inferred and not directly determined motifs, so they should be considered as preliminary.

We had considered using TF binding motifs previously, and now we gave a try to analyzing potential transcription factor binding sites in divergent promoters. We find that there are no P. ostreatus transcription factors for which motifs based on direct evidence are available; rather, all P. ostreatus motifs are based on extrapolations from experimentally determined motifs (typically in Neurospora crassa). Therefore, to avoid too general motifs, we used only those where at least 5 nucleotides show at least 80% expected frequency in the PWM-s. This left us with 158 motifs (126 excluded). High motif binding score (>=4) and self-rate (>=0.9) were also required to ignore false positive hits. Different binding ability and lack of binding in one of the parental genomes were counted for each promoter. We found that genes with allele specific expression (ASE S2 and S4) show significantly higher differences in motif binding (lacking motifs, or different binding ability) than non-ASE genes (Fig. A1). These observations show that, not only promoter divergence, but differential predicted TF binding ability is also more common among ASE genes than among non-ASE genes. This supports our conjecture that ASE arises from cis-regulatory divergence.

Fig A1: The left plot below shows the number of cases when the promoter of one allele of an allele pair in the two parent genomes has, but the other lacks a motif. The right plot shows the same in terms of difference in binding score.

We could find examples, such as the allele specific expression of PleosPC15_2_1031042, a Hemerythrin-like (IPR012312) protein which might be regulated by the conserved c2h2 transcription factor, containing zinc finger domain of the C2H2 type (Fig. A2). C2h2 has already been proved to be important during the initiation of primordia formation with targeted gene inactivation (Ohm et al 2011, https://pubmed.ncbi.nlm.nih.gov/21815946/). A binding site of c2h2 was detected in the upstream region of PleosPC15_2_1031042. There is a mismatch in the inferred binding motif which causes a reduced binding score in PC15 (Fig. A2/c). Indeed the PC9 nuclei contribute better to the total expression of this gene.

Despite this, and other (not shown) examples that we have found, we were not convinced about the reliability of this approach. There are many assumptions in this analysis, the positional weight matrices (PWM) that we used, are all based on indirect evidence, high number of loci these PWMs identify, uncertainty in the position of binding site from transcriptional start site, relation of difference in binding motif and expressional changes. We consider these factors to potentially contribute too much noise to the analyses for these to be robust, therefore, we are hesitant to include these results in the ms.

Fig A2: An example for promoter divergence a) expression of c2h2 transcription factor (TF) in P. ostreatus. b) allele-specific expression pattern of PleosPC15_2_1031042 from the two parental genomes. c) inferred binding motif of c2h2 TF and a detected potential binding site in the upstream region of PleosPC15_2_1031042 gene.

Reviewer #2 (Public Review):

The evolution of complex multicellularity represents a major developmental reprogramming, and comparing related species which differ in multicellular structures may shed light on the mechanisms involved. Here, the authors compare species of Basidiomycete fungi and focus on analyzing developmental transcriptomes to identify patterns across species. Deep RNA-Seq data is generated for two species, P. ostreatus and Pt. gracilis, sampling different developmental stages. The authors report conflicting evidence for a "developmental hourglass" using a weighted transcription index vs gene age categories. There is substantial allele-specific expression in P. ostreatus, and these genes tend to have a more recent origin, have more divergent upstream regions and coding sequences, and are enriched for developmentally regulated transcripts. Antisense transcripts have low overlap with coding regions and low conservation, and a subset show a positive or negative correlation with the overlapping gene. Comparison to a species without complex multicellular development is used to further classify the developmental program.

Overall the new transcriptional data and extensive analysis provide a thorough view of the types of transcripts that appear differentially regulated, their age, and associated gene function enrichment. The gene sets identified from this analysis as well as the potential to re-analyze this data will be useful to the community studying multicellularity in fungi. The primary insights drawn in this study relate to the dating of the developmental transcriptome, however some patterns observed with young genes and noncoding transcripts are primarily reflective of expected patterns of evolutionary time.

We appreciate the Reviewer’s nice words on our ms, we think the revised version has substantial improvements in many aspects listed above.

Reviewer #3 (Public Review):

Fungi are unique in forming complex 3D multicellular reproductive structures from 2D mycelium filaments, a property used in this paper to study the genetic changes associated with the evolution of complex 3D multicellularity. The manuscript by Merenyi et al. investigates the evolution of gene expression and genome regulation during the formation of reproductive structures (fruiting bodies) in the Agaricomycetes lineage of Fungi. Transcriptome and multicellularity evolution are very exciting fundamental questions in biology that only become accessible with recent technological developments and the appropriate analysis framework. Important perspectives include understanding how genes acquire new functions and what role plays transcriptional regulation in adaptation. The study gathers a very useful dataset to this end, and relies on generally relevant hypotheses-driven analyses.

Analysis of fruiting body transcriptome in nine species revealed that prediction from the development hourglass model (that young genes are expressed in early and late but not intermediate phases of development) verified only in a few species, including Pleurotus ostreatus. An allele-specific expression (ASE) analysis in P. ostreatus showed that young genes frequently show ASE during fruiting body development. A comparative analysis with C. neoformans, which reproduces sexually without forming fruiting body, indicates that young and old (but not intermediate) genes are likely involved specifically in fruiting body morphogenesis. A number of underlying hypothesis could be presented better, and importantly the connection between the various analyses did not appear obvious to me. Some hypotheses and reasoning therefore need clarification. Some important results from the analyses are not provided and not commented, although they are required to fully meet the manuscript's objectives.

We appreciate the Reviewer’s suggestions and have revised the ms as explained below.

1. I do not clearly see the connection between the developmental hourglass model studied in the first part of the ms, and the allele-specific expression patterns in the second half of the ms. Which "phase" of the hourglass is expected to contain true CM-related genes (by contrast to general sexual processes)? Was P. ostreatus chosen for the ASE analysis because evidence for a developmental hourglass pattern was detected in this species? The conclusion that "evolutionary age predicts, to a large extent, the behaviour of a gene in the CM transcriptome" was established thanks to ASE in P. ostreatus, which was also found to be rather an exception for conforming to the hourglass model of developmental evolution. To what extent is this conclusion transferable to other Agaricomycete/fungal species?

We chose P. ostreatus because this is the only species for which the genomes of both parental strains (PC9 and PC15) are available. Although the hourglass concept is indeed a central hypothesis in animal developmental biology (though see recent critiques some (Piasecka et al 2013), our results suggest that it simply does not generally apply to fungal development. This may be due to the unique developmental mechanisms of fungi, or the independent origin(s) of CM in fungi. Our ms might have been misleading in this respect, in the revision we clarify that the ASE and hourglass analyses are independent of each other. Our interpretation of the hourglass results is that this model is not or hardly applicable for fungal development and the fact that P. ostreatus was the only species that in fact showed an hourglass did not drive our selection of this species. We inserted a note on this in the ms.

1. The authors acknowledge that fruiting body-expressed genes may relate either to CM or to more general sexual functions, and that disentangling these functions is a major challenge in their study. An overview of which gene was assigned to which function is not explicit in the ms (proposed to be described in a separate publication). Do these functional gene classes show distinct transcriptome evolution patterns (hourglass model, ASE...)?

We made accessible the complete list of CM-related genes and genes with more general sexual functions in Table S2/b-c. Due to length restrictions, we do not discuss many or each of these genes here, but provided gene ontology-based overviews (Fig 8/c-d, from lines 631). To answer the question whether CM vs shared genes show distinct transcriptomic patterns, we analyzed ASE, NATs and the hourglass model separately for CM-specific and shared genes. as follows:

-hourglass: We calculated and visualised the TAI for CM-specific and Shared gene sets of P. ostreatus separately. The average value of TAI decreased a lot in Shared genes possibly due to the overrepresentation of ancient genes here, but the patterns remained similar to the original, which imply that not simply one or the other gene set drives these patterns (Fig A3).

Fig A3: Transcriptome Age Index for CM-specific and Shared gene sets of P. ostreatus separately

-ASE: As we detailed in the ms, allele specific expression occurs mainly in young genes. Indeed, only 13.1% of ASE genes belong to the conserved gene sets (CMspecific: 200 and Shared: 144). Although there are more ASE genes (>2FC) among CM-specific genes, they are still underrepresented compared to young genes that are neither shared, nor CM-specific. This indicates that ASE is generally a feature of non-conserved genes and is not particularly characteristic for either conserved or CM-specific genes.

-NAT: We found that 17.3% of CM-specific (141 genes) and 18.3% of Shared genes (165 genes) overlap with antisense transcripts. Since these numbers don't differ substantially from 17.6%, which is the proportion of NATs corresponding to all protein coding genes, it implies an independent occurrence between NATs and these gene conservation groups.

3.) As far as I understand, major functions of the fruiting body transcriptome are either CM or general sexual functions. Could these genes, notably those showing ASE, play a role in general processes other than sexual development (hyphal growth, environment sensing, cell homeostasis, pathogenicity)?

Certainly, ASE might also occur in genes related to these processes. However, the processes mentioned by the Reviewer are likely associated with very conserved genes (except pathogenicity, which we can’t examine here) and our results suggest that ASE is more typical of young genes that are under weak selection. We detected ASE in 931/343 (S2/S4 genes) genes expressed in the vegetative mycelium stage of P. ostreatus. We also note that by the definition of developmentally regulated genes, we do not expect very basic fungal processes, like hyphal growth to be among the functions of the genes we identified. Genes related to such basic (housekeeping) processes usually (exceptions exist) show flat expression profiles (because they are equally important in mycelia and all fruiting body stages) and will not be picked up by our pipelines for identifying shared developmentally regulated genes.

1. As stated by the authors, "the goal of this study was to systematically tease apart the components and driving forces of transcriptome evolution in CM fungi". What drives the interesting ASE pattern discovered however remains an open question at the end of the ms. The authors appropriately discuss that these patterns could be either adaptive or neutral but there is no direct evidence for any scenario in P. ostreatus. Is the expression of (some of) the young genes showing ASE required for CM? one or two case studies would allow providing support for such scenarios.

We respectfully disagree. We provide evidence that the driving force of ASE is promoter divergence (and consequently differential transcription factor binding) in genes in which it is tolerated (see conclusions, lines 708-712). Our results suggest that ASE is mostly a neutrally arising phenomenon. To get to the mechanistic bases of how promoter divergence can cause ASE (following the suggestion of Reviewer 1), we analysed putative, inferred transcription factor binding motifs in P. ostreatus and found that ASE genes had more divergence in putative TF binding sites. However, it is important to emphasise that all TF motifs we analyzed are inferred motifs and therefore these results are indicative at best.

Reviewer #4 (Public Review):

This work develops a comparative framework to test genes which support complex morphological structures and complex multicelluarity. This expands beyond simple gene sharing and phylogenomics by incorporating comparison of gene expression profiling of development of multicellular structures during sexual reproduction. This approach tests the hypothesis that genes underlying sexual reproductive structure formation are homologous and the molecular evolutionary processes that control transcriptome evolution which underlie complex multicellularity.

The approaches used are appropriate and employ modern comparative and transcriptome analyses to example allele specific expression, and evaluate an age of the evolutionary ages of genes. This work produced additional new RNAseq to examine developmental processes and combined it with existing published data to contrast fungi with either complex morphologies or yeast forms.

The strengths of work are well selected comparison organisms and efforts to have developmental stages which are appropriate comparisons.

We appreciate the Reviewer’s positive comments.

Weakness could be pointed to in how the NAT descriptions are interesting it isn't clear how they link directly to morphology variation or development. I am unclear if these are arising from new de novo promotors, are ferried by transposable elements, or if any other understanding of their genesis indicates they are more than very recent gains in a species for the most part and not part of any conserved developmental process (outside a few exemplars).

Originally, we assayed natural antisense transcripts (NAT) based on the assumption that they regulate developmental processes (e.g. Kim et al 2018 https://doi.org/10.1128/mBio.01292-18). Our analyses showed that although NATs are abundant in CM transcriptomes of fungi, they show no homology across species and so are unlikely to drive conserved developmental processes, which we are after in this ms. Rather, our data are compatible with most (but likely not all) NATs being transcriptional noise, arising from novel or random promoters. We therefore shortened this section and moved much of it to the Appendix 1.

The impact of this work will reside in how gene age intersects with variability and relative importance in CM. it will be interesting to see future work examine the functions of these genes and test how allele specific expression and specific alleles are contributing to the formation of these tissues and growth forms. I am still not sure if molecular mechanisms of how high variability in gene expression is still producing relatively uniform morphologies, or if it isn't quantification of morphological variation would be nice to link to whether ASE underlie that.

We agree that allele specific expression could influence morphologies significantly, but investigating that is beyond the scope of the current work (it would require a population genomics project). More direct evidence on allelic differences can be seen in monokaryon phenotypes, which only express one of the parental alleles. Phenotypic differences are obvious in the mycelium of the two parental monokaryons : the mycelium of PC9 is more fluffy and grows faster than that of PC15. This was reported recently by Lee et al 2021 (https://doi.org/10.1093/g3journal/jkaa008). We agree with the Reviewer that this is a very exciting future research direction.

To my read of the work, the authors achieved their goals and confirmed hypothesis about the age of genes and the variability of gene expression. I still feel there is some clarity lost in whether the findings across the large number of species compared here help inform predictions or classifications of types of genes which either have ASE or are implicated in CM. This is really work for the future as the authors have provided a detailed analysis and approach that can fuel further direction in this research area.

To address this issue we reworked the ms to make connections between ASE and CM clearer. Because ASE appears based on our results to (mostly) arise neutrally, predictions for other species are expected to be hard. On the other hand, we think we can make confident predictions on what types of genes are implicated in CM in other species, at least for conserved aspects of fruiting body development.

Author Response

Reviewer #1 (Public Review):

In this study, the authors set out to clarify the relationship between brain oscillations and different levels of speech (syllables, words, phrases) using MEG. They presented word lists and sentences and used task instructions to attempt to focus listeners' attention on different levels of linguistic analysis (syllables, words, phrases).

1) I came away with mixed feelings about the task design: following each stimulus (sentence or word list), participants were asked to (a) press a button (i.e. nothing related to what they heard, (b) indicate which of two syllables was heard, (c) indicate which of two words was heard, (d) indicate which pair of words was present in the correct order. This task is the critical manipulation in the study, as it is intended to encourage (or in the authors' words, "require") participants to focus on different timescales of speech (syllable, word, and phrase, respectively). I very much like the idea of keeping the physical stimuli unchanged, and manipulating attention through task demands - an elegant and effective approach. At the same time, I have reservations about the degree to which these task instructions altered attention during listening. My intuition is that, if I were a participant, I would just listen attentively, and then answer the question about the specific level. For example, I don't know that knowing I would be doing a "word pair" task, I would be attending at a slower rate than a "word" task, as in both cases I would be motivated to understand all of the words in the sentence. I fully acknowledge my introspection (n=1) may be flawed here, but nevertheless, any additional support validating the effect of these instructions would help the interpretation of the MEG results.

The reviewer points out that to do any task on sentences (such as a word task and a syllable task) participants’ strategy could be to understand the full meaning of the sentence and infer the lower level properties based on the understanding of the full sentence. We fully share this introspection, which would suggest that extracting sentence meaning is partly automatic (or at least a default mode of processing) and independent of the behavioral relevance. While the reviewer sees this as a downside of the design, this is part of what our study tried to disentangle (automatic versus task-dependent processing at lower frequency time-scales). If, as the reviewer points out, all processing of sentences would be automatic we should not find any effect of task (as the task should not affect the tracking response at all). We found that overall the tracking response is robust to task-induced manipulation of attention – the main effect that MI to phrases is higher for sentences than for word lists is robust across passive and task conditions. But that is not the whole story on the source level, where we do find some task effects, which indicates that task instructions do matter. This means that participants changed their strategy depending on the instructions, but that overall, tracking of linguistic structures such as phrases is automatic. We show that for the IFG MI phrasal time scales are tracked stronger during the phrase task versus the other tasks. This is also reflected in stronger STG-IFG connectivity during the phrasal versus passive task. These results speak against the interpretation of the reviewer that “task instructions“ do not “ altered attention during listening”. While there are these subtle task differences, especially in IFG, overall our findings do speak for an automatic tracking of phrasal rate structure in sentences independent of task. We therefore concluded that “automatic understanding of linguistic information, and all the processing that this entails, cannot be countered to substantially change the consequences for neural readout, even when explicitly instructing participants to pay attention to particular time-scales” (line 548-549).

The analysis steps generally seem sensible and well-suited to answering the main claims of the study. Controlling for power differences between conditions through matching was a nice feature.

2) I had a concern about accuracy differences (as seen in Figure 1) across stimulus materials and tasks. In particular, for the phrase task, participants were more accurate for sentence stimuli than word list stimuli. I think this makes a lot of sense, as a coherent sentence will be easier to remember in order than a list of words. But, I did not see accuracy taken into account in any of the analyses. These behavioral differences raise the possibility that the MEG results related to the sentence > word list contrast in phrases (which seems one of the most interesting findings in IFG) simply reflect differences in accuracy.

With the caveat of the concern regarding accuracy differences, the research goals were clear and the conclusions were generally supported by the analyses.

Thank you for pointing this out. We have now taken accuracy into account in our analysis. It did not change any of our main findings or conclusions, and strengthened the argument that tracking of phrases in sentences vs. word lists is stronger. The influence of task difficulty is a relevant point to investigate (also see point 1 of reviewer 2 and point 4 of reviewer 3). To do so we added accuracy (per participant per condition) as a factor in the mixed model (as well as all interactions with task and condition) for the MI, power, and connectivity analyses at the phrasal rate/delta band. Note that as for the passive task there is no accuracy, we removed the passive task from the analyses. We could also only run models with random intercepts (not random slopes), due to the reduced number of degrees of freedom when adding the factor accuracy to the models.

For the MI analysis we only found an effect in MTG. Specifically, there was a three-way interaction between task, condition and accuracy (F(2, 91.9) = 3.4591, p = 0.036). To follow up on this three-way interaction we split the data per task. The condition*accuracy interaction was only (uncorrected) significant for the word combination task (F(1,24.8) = 5.296, p = 0.03 (uncorrected)) and not for any other task (p>0.1). In the word combination task, we found that the difference between sentences and word lists was the strongest at high accuracies (see below figure the predicted values of the model). One way to interpret this finding is that stronger phrasal-rate MI tracking in MTG promotes phrasal-rate processing (as indicated by accuracy) more in sentences than in word lists.

MEG – behavioral performance relation. A) Predicted values for the phrasal band MI in the MTG for the word combination task separately for the two conditions. B) Predicted values for the delta band WPLI in the STG-MTG connection separately for the two conditions. Error bars indicate the 95% confidence interval of the fit. Colored lines at the bottom indicate individual datapoints.

For power we did not find any effect of accuracy. For the connectivity analysis we found in the STG-MTG connectivity a significant conditionaccuracy interaction (F(1, 80.23)=5.19, p = 0.025). The conditionaccuracy interaction showed that lower accuracies were generally associated with stronger differences between the sentences and word lists (see figure; the opposite of the MI analysis). Thus, functional connections in the delta band are stronger during sentence processing when participants have difficulty with the task (independent of the task performed). This could indicate that low-frequency connections are more relevant for the sentence than the word list condition (as the reviewer also indicated in point 1).

After correcting for accuracy there was also a significant task condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005 corrected), but not for the other tasks (p>0.1).

We added the results of the accuracy analyses in the main manuscript as well as adding a dedicated section in our discussion section (page 21-22). Adding accuracy did not remove any of the effects we report in the original analyses. Therefore, none of these finding change the interpretation of the results as the task still had an influence on the MI responses of MTG and IFG. The effect of accuracy in the MTG refined the results showing that the effect was strongest there for participants with high accuracies. This relationship suggests a functional role of tracking through phase alignment for understanding phrasal structure.

The methods now read: “MEG-behavioural performance analysis: To investigate the relation between the MEG measures and the behavioural performance we repeated the analyses (MI, power, and connectivity) but added accuracy as a factor (together with the interactions with the task and condition factor). As there is no accuracy for the passive task, we removed this task from the analysis. We then followed the same analyse steps as before. Since we reduced our degree of freedom, we could however only create random intercept and not random slope models”.

The results now read: “MEG-behavioural performance relation. We found for the MI analysis a significant effect of accuracy only in the MTG. Here, we found a three-way interaction between accuracy task condition (F(2, 91.9) = 3.459, p = 0.036). Splitting up for the three different tasks we found only an uncorrected significant effect for the condition accuracy interaction for the phrasal task (F(1, 24.8) = 5.296, p = 0.03) and not for the other two tasks (p>0.1). In the phrasal task, we found that when accuracy was high, there was a stronger difference between the sentence and the word list condition compared to when accuracy was low, with stronger accuracy for the sentence condition (Figure 7A).

No relation between accuracy and power was found. For the connectivity analysis we found a significant condition accuracy interaction for the STG-MTG connection (F(1,80.23) = 5.19, p = 0.025; Figure 7B). Independent of task, when accuracy was low the difference between sentence and word lists was stronger with higher WPLI fits for the sentence condition. After correcting for accuracy there was also a significant task condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005), but not for the other tasks (p>0.1).”

The discussion now reads: “We found that across participants both the MI and the connectivity in temporal cortex influenced behavioural performance. Specifically, MTG-STG connections were, independent of task, related to accuracy. There was higher connectivity between MTG and STG for sentences compared to word lists at low accuracies. At high accuracies, we found that stronger MTG tracking at phrasal rates (measured with MI) for sentences compared to word lists during the word combination task. These results suggest that indeed tracking of phrasal structure in MTG is relevant to understand sentences compared to word lists. This was reflected in a general increase in delta connectivity differences when the task was difficult (Figure 7B). Participants might compensate for the difficulty using phrasal structure present in the sentence condition. When phrasal structure in sentences are accurately tracked (as measured with MI) performance is better when these rates are relevant (Figure 7A). These results point to a role for phrasal tracking for accurately understanding the higher order linguistic structure in sentences even though more research is needed to verify this. It is evident that the connectivity and tracking correlations to behaviour do not explain all variation in the behavioural performance (compare Figure 1 with 3). Plainly, temporal tracking does not explain everything in language processing. Besides tracking there are many other components important for our designated tasks, such as memory load and semantic context which are not captured by our current analyses.”

Reviewer #2 (Public Review):

In a MEG study, the authors investigate as their main question whether neural tracking at the phrasal time scale reflects linguistic structure building (testing different conditions: sentences vs. word-lists) or an attentional focus on the phrasal time scale (testing different tasks, passive listening, syllable task, word task, word combination/phrasal scale task). They perform the following analyses at brain areas (ROIs: STG, IFG, MTG) of the language network: (1) Mutual information (MI) between the acoustic envelope and the delta band neuronal signals is analyzed. (2) Power in the delta band is analyzed. (3) Connectivity is analyzed using debiased WPLI. For all analyses, linear mixed-models are separately conducted for each ROI. The main finding is that the sentence compared to the word-list condition is more strongly tracked at the phrasal scale (MI). In STG the effect was task-independent; in MTG the effect only occurred for active tasks; and in IFG additionally, the word-combining/phrasal scale task resulted in higher tracking compared to all other tasks. The authors conclude that phrasal scale neural tracking reflects linguistic processing which takes place automatically, while task-related attention contributes additionally at IFG (interpreted as combinatorial hub involved in language and non-language processing). The findings are stable when power differences are controlled. The connectivity analysis showed increased connectivity in the delta band (phrasal time scale) between IFG-STG in the phrasal-scale compared to the passive task (adding to the IFG MI findings). (Additionally, they separately analyze neural tracking at the syllabic and word time scale, which however is not in the main focus).

Major strength/weaknesses of the methods and results:

1) A major strength of the results is that part of them replicate the authors' earlier findings (i.e. higher tracking at the phrasal time scale for sentences compared to word-lists; Kaufeld et al., 2020), while they complement this earlier work by showing that the effects are due to linguistic processing and not to an attentional focus on the phrasal time scale due to the task (at least in STG and MTG; while the task plays a role for the IFG tracking). Another strength is that a power control analysis is applied, which allows excluding spurious results due to condition differences in power. A weakness of the method is that analyses were applied separately per ROI, and combined across correct/incorrect trials (if I understood correctly), no trial-based analysis was conducted (which is related to how MI is computed). Furthermore, several methodological details could be clarified in the manuscript.

The authors achieved their aims by providing evidence that neuronal tracking at the phrasal time scale in STG and MTG depends on the presence of linguistic information at this scale rather than indicating an attentional focus on this time scale due to a specific task. Their results support the conclusion. Results would be strengthened by showing that these effects are not impacted by different amounts of correct/incorrect trials across conditions (if I understood that correctly).

We thank the reviewer for her comments. It is correct that we collapsed across the correct and incorrect trials. This had various reasons (also see point 2 and 9 of reviewer 1 and point 4 of reviewer 3). First, our tasks function solely to direct participants’ attention to the various linguistic representations (syllables, words, phrases) and the timescales that they occur on. The three tasks are in a sense more control tasks to study the tracking response, and manipulate attention as tracking during spoken language comprehension occurs, rather than a case where the neural response to the tasks is itself to be studied. For example, in a typical working memory paradigm, it is only during correct trials that the relevant cognitive process occurs. In contrast, in our paradigm, it is likely that that spoken stimuli are heard and processing, in other words, sentence comprehension and word list perception occur, even during incorrect trials in the syllable condition. As such, we do not expect MI tracking responses to explain the behavioral data. However, we agree it is crucially important to show that MI differences are not a function of task performance differences.

Second, there are clear differences in difficulty level of the trials within conditions. For example, if the target question was related to the last part of the audio fragment, the task was much easier than when it was at the beginning of the audio fragment. In the syllable task, if syllables also were (by chance) a part-word, the trial was also much easier. If we were to split up in correct and incorrect we would not really infer solely processes due to accurately processing the speech fragments, but also confounded the analysis by the individual difficulty level of the trials.

To acknowledge this, we added this limitation to the methods. The methods now reads: “Note that different trials within a task were not matched for task difficulty. For example, in the syllable task syllables that make a word are much easier to recognize than syllables that do not make a word. Additionally, trials pertaining to the beginning of the sentence are more difficult than ones related to the end of the sentence due to recency effects.”.

To still investigate if overall accuracy influenced the results we did add accuracy (across participants) to the mixed models. Note that as for the passive task there is no accuracy, we removed the passive task from the analyses. We could also only run models with random intercepts (not random slopes), due to the reduced number of degrees of freedom when adding the factor accuracy to the models.

For the MI analysis we only found an effect in MTG. Specifically, there was a three-way interaction between task, condition and accuracy (F(2, 91.9) = 3.4591, p = 0.036). To follow up on this three-way interaction we split the data per task. The condition*accuracy interaction was only (uncorrected) significant for the word combination task (F(1,24.8) = 5.296, p = 0.03 (uncorrected)) and not for any other task (p>0.1). In the word combination task, we found that the difference between sentences and word lists was the strongest at high accuracies (see on the right attached figure the predicted values of the model). One way to interpret this finding is that stronger phrasal-rate MI tracking in MTG promotes phrasal-rate processing (as indicated by accuracy) more in sentences than in word lists.

For power we did not find any effect of accuracy. For the connectivity analysis we found in the STG-MTG connectivity a significant conditionaccuracy interaction (F(1, 80.23)=5.19, p = 0.025). The conditionaccuracy interaction showed that lower accuracies were generally associated with stronger differences between the sentences and word lists (see figure below; the opposite of the MI analysis). Thus, functional connections in the delta band are stronger during sentence processing when participants have difficulty with the task (independent of the task performed). This could indicate that low-frequency connections are more relevant for the sentence than the word list condition.

MEG – behavioral performance relation. A) Predicted values for the phrasal band MI in the MTG for the word combination task separately for the two conditions. B) Predicted values for the delta band WPLI in the STG-MTG connection separately for the two conditions. Error bars indicate the 95% confidence interval of the fit. Colored lines at the bottom indicate individual datapoints.

After correcting for accuracy there was also a significant task*condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005 corrected), but not for the other tasks (p>0.1).

We added the results of the accuracy analyses in the main manuscript as well as adding a dedicated section in our discussion section (page 21-22). Adding accuracy did not remove any of the effects we report in the original analyses. Therefore, none of these finding change the interpretation of the results as the task still had an influence on the MI responses of MTG and IFG. The effect of accuracy in the MTG refined the results showing that the effect was strongest there for participants with high accuracies. This relationship suggests a functional role of tracking through phase alignment for understanding phrasal structure.

The methods now read: “MEG-behavioural performance analysis: To investigate the relation between the MEG measures and the behavioural performance we repeated the analyses (MI, power, and connectivity) but added accuracy as a factor (together with the interactions with the task and condition factor). As there is no accuracy for the passive task, we removed this task from the analysis. We then followed the same analyse steps as before. Since we reduced our degree of freedom, we could however only create random intercept and not random slope models”.

The results now read: “MEG-behavioural performance relation. We found for the MI analysis a significant effect of accuracy only in the MTG. Here, we found a three-way interaction between accuracytaskcondition (F(2, 91.9) = 3.459, p = 0.036). Splitting up for the three different tasks we found only an uncorrected significant effect for the condition*accuracy interaction for the phrasal task (F(1, 24.8) = 5.296, p = 0.03) and not for the other two tasks (p>0.1). In the phrasal task, we found that when accuracy was high, there was a stronger difference between the sentence and the word list condition compared to when accuracy was low, with stronger accuracy for the sentence condition (Figure 7A).

No relation between accuracy and power was found. For the connectivity analysis we found a significant conditionaccuracy interaction for the STG-MTG connection (F(1,80.23) = 5.19, p = 0.025; Figure 7B). Independent of task, when accuracy was low the difference between sentence and word lists was stronger with higher WPLI fits for the sentence condition. After correcting for accuracy there was also a significant taskcondition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005), but not for the other tasks (p>0.1).”

The discussion now reads: “We found that across participants both the MI and the connectivity in temporal cortex influenced behavioural performance. Specifically, MTG-STG connections were, independent of task, related to accuracy. There was higher connectivity between MTG and STG for sentences compared to word lists at low accuracies. At high accuracies, we found that stronger MTG tracking at phrasal rates (measured with MI) for sentences compared to word lists during the word combination task. These results suggest that indeed tracking of phrasal structure in MTG is relevant to understand sentences compared to word lists. This was reflected in a general increase in delta connectivity differences when the task was difficult (Figure 7B). Participants might compensate for the difficulty using phrasal structure present in the sentence condition. When phrasal structure in sentences are accurately tracked (as measured with MI) performance is better when these rates are relevant (Figure 7A). These results point to a role for phrasal tracking for accurately understanding the higher order linguistic structure in sentences even though more research is needed to verify this. It is evident that the connectivity and tracking correlations to behaviour do not explain all variation in the behavioural performance (compare Figure 1 with 3). Plainly, temporal tracking does not explain everything in language processing. Besides tracking there are many other components important for our designated tasks, such as memory load and semantic context which are not captured by our current analyses.”

The findings are an important contribution to the ongoing debate in the field whether neuronal tracking at the phrasal time scale indicates linguistic structure processing or more general processes (e.g. chunking).

Reviewer #3 (Public Review):

This manuscript presents a MEG study aiming to investigate whether neural tracking of phrasal timescales depends on automatic language processing or specific tasks related to temporal attention. The authors collected MEG data of 20 participants as they listened to naturally spoken sentences or word lists during four different tasks (passive listening vs. syllable task vs. word tasks vs. phrase task). Based on mutual information and Connectivity analysis, the authors found that (1) neural tracking at the phrasal band (0.8-1.1 Hz) was significantly stronger for the sentence condition compared to the word list condition across the classical language network, i.e., STG, MTG, and IFG; (2) neural tracking at the phrasal band was (at least tend significantly) stronger for phrase task than other tasks in the IFG; (3) the IFG-STG connectivity was increased in the delta-band for the phrase task. Ultimately, the authors concluded that neural tracking of phrasal timescales relied on both automatic language processing and specific tasks.

Overall, this study is trying to tackle an interesting question related to the contributing factors for neural tracking of linguistic structures. The study procedure and analyses are well executed, and the conclusions of this paper are mostly well supported by data. However, I do have several major concerns.

1. The title of the manuscript uses the description "tracking of hierarchical linguistic structure". In general, hierarchical linguistic structures involve multiple linguistic units with different timescales, such as syllables, words, phrases, and sentences. In this study, however, the main analysis only focused on the phrasal band (0.8-1.1 Hz). It seemed that there was no significant stimulus- or task-effect on the word band or syllabic band (supplementary figures). Therefore, it is highly recommended that the authors modify the related descriptions, or explain why neural tracking of phrases can represent neural tracking of hierarchical linguistic structures in the current study.

We thank the reviewer for this comment. We meant to refer to the task manipulation directing attention to different levels of representation across the linguistic hierarchy. We have changed the title to “Neural tracking of phrases during spoken language comprehension is automatic and task-dependent.” We hope this resolves any inadvertent confusion we created. Furthermore, throughout the manuscript we ensure to talk about effect occurring for phrasal tracking at low frequency bands at not across any hierarchical linguistic structure. We agree that our findings cannot speak for any task-dependent effects along the hierarchy, only that at the phrasal level there is a difference between sentences and word lists.

1. In Methods, the authors employed MI analyses on three frequency bands: 0.8-1.1 Hz for the phrasal band, 1.9-2.8 Hz for the word band, and 3.5-5.0 Hz for the syllabic band (line 191-192). As the timescales of linguistic units are various and overlapped in natural speech, I wonder how the authors define the boundaries of these frequency bands, and whether these bands are proper for the naturally spoken stimuli in the current study. These important details should be clarified.

The frequency bands of the MI analysis were based on the stimuli, or in other words, are data driven. They reflect the syllabic, word, and phrasal rates in our stimulus set (calculated in Kaufeld et al., 2020). They were calculated by annotating the sentences by syllables, words, and phrasal and converting the rate of the linguistic units to frequency ranges. The information has been added to the manuscript. We acknowledge that unlike our stimulus set in natural speech the boundaries of these bands can overlap and now also state this (“While in our stimulus set the boundaries of the linguistic levels did not overlap, in natural speech the brain has an even more difficult task as there is no one-to-one match between band and linguistic unit [26]”, line number 211-213).

1. What is missing in the manuscript are the explanations of the correlation between behavioral performance and neural tracking. In Results, the behavioral performance shows significant differences across the active tasks (Figure 1), but the MI differences across the tasks are relatively weak in IFG (Figure 3). In addition, the behavioral performance only shows significant differences between the sentence and word list conditions during the phrasal task, but the MI differences between the conditions are significant in MTG during the syllabic, word, and phrasal tasks. Explanations for these inconsistent results are expected.

We answer this point together with point 4 below where we analyze the behavioral performance and the MEG responses.

1. Since the behavioral performance of these active tasks is likely related to the temporal attention to relevant timescales of different linguistic units, I wonder whether there exist underlying neural correlates of behavioral performance (e.g., significant correlation between performance and mutual information). If so, it may be interesting and bring a new bright spot for the current study.

The influence of task difficulty is a relevant point to investigate (also see point 1 of reviewer 2 and point 4 of reviewer 3). To do so we added accuracy (per participant per condition) as a factor in the mixed model (as well as all interactions with task and condition) for the MI, power, and connectivity analyses at the phrasal rate/delta band. Note that as for the passive task there is no accuracy, we removed the passive task from the analyses. We could also only run models with random intercepts (not random slopes), due to the reduced number of degrees of freedom when adding the factor accuracy to the models.

For the MI analysis we only found an effect in MTG. Specifically, there was a three-way interaction between task, condition and accuracy (F(2, 91.9) = 3.4591, p = 0.036). To follow up on this three-way interaction we split the data per task. The condition*accuracy interaction was only (uncorrected) significant for the word combination task (F(1,24.8) = 5.296, p = 0.03 (uncorrected)) and not for any other task (p>0.1). In the word combination task, we found that the difference between sentences and word lists was the strongest at high accuracies (see the below figure the predicted values of the model). One way to interpret this finding is that stronger phrasal-rate MI tracking in MTG promotes phrasal-rate processing (as indicated by accuracy) more in sentences than in word lists.

MEG – behavioral performance relation. A) Predicted values for the phrasal band MI in the MTG for the word combination task separately for the two conditions. B) Predicted values for the delta band WPLI in the STG-MTG connection separately for the two conditions. Error bars indicate the 95% confidence interval of the fit. Colored lines at the bottom indicate individual datapoints.

For power we did not find any effect of accuracy. For the connectivity analysis we found in the STG-MTG connectivity a significant conditionaccuracy interaction (F(1, 80.23)=5.19, p = 0.025). The conditionaccuracy interaction showed that lower accuracies were generally associated with stronger differences between the sentences and word lists (see figure attached; the opposite of the MI analysis). Thus, functional connections in the delta band are stronger during sentence processing when participants have difficulty with the task (independent of the task performed). This could indicate that low-frequency connections are more relevant for the sentence than the word list condition.

After correcting for accuracy there was also a significant task*condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005 corrected), but not for the other tasks (p>0.1).

We added the results of the accuracy analyses in the main manuscript as well as adding a dedicated section in our discussion section (page 21-22). Adding accuracy did not remove any of the effects we report in the original analyses. Therefore, none of these finding change the interpretation of the results as the task still had an influence on the MI responses of MTG and IFG. The effect of accuracy in the MTG refined the results showing that the effect was strongest there for participants with high accuracies. This relationship suggests a functional role of tracking through phase alignment for understanding phrasal structure.

While the findings can explain some behavioral effects, we agree with the reviewer that the behavioral results and the MI results don’t align. We note that our use of tasks to guide attention to different timescales and linguistic representations differs from the use of, for example, a working memory task where only the correct trials contain the relevant cognitive process. In working memory type paradigms, the MEG data should indeed explain the behavioral response. Our study was designed to test for effects of task demands on the neural tracking response to speech and language. As we are only using the tasks to control attention, we do not attempt to explain behavior through the MEG data or differences in MI.

Thus, the phrasal tracking cannot explain all of the behavioral results (point 3). It is at this point unclear what could have caused this effect, but it quite likely that neural sources outside the speech and language ROIs we selected are in play. We discuss this now.

The methods now read: “MEG-behavioural performance analysis: To investigate the relation between the MEG measures and the behavioural performance we repeated the analyses (MI, power, and connectivity) but added accuracy as a factor (together with the interactions with the task and condition factor). As there is no accuracy for the passive task, we removed this task from the analysis. We then followed the same analyse steps as before. Since we reduced our degree of freedom, we could however only create random intercept and not random slope models”.

The results now read: “MEG-behavioural performance relation. We found for the MI analysis a significant effect of accuracy only in the MTG. Here, we found a three-way interaction between accuracytaskcondition (F(2, 91.9) = 3.459, p = 0.036). Splitting up for the three different tasks we found only an uncorrected significant effect for the condition*accuracy interaction for the phrasal task (F(1, 24.8) = 5.296, p = 0.03) and not for the other two tasks (p>0.1). In the phrasal task, we found that when accuracy was high, there was a stronger difference between the sentence and the word list condition compared to when accuracy was low, with stronger accuracy for the sentence condition (Figure 7A).

No relation between accuracy and power was found. For the connectivity analysis we found a significant conditionaccuracy interaction for the STG-MTG connection (F(1,80.23) = 5.19, p = 0.025; Figure 7B). Independent of task, when accuracy was low the difference between sentence and word lists was stronger with higher WPLI fits for the sentence condition. After correcting for accuracy there was also a significant taskcondition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005), but not for the other tasks (p>0.1).”

The discussion now reads: “We found that across participants both the MI and the connectivity in temporal cortex influenced behavioural performance. Specifically, MTG-STG connections were, independent of task, related to accuracy. There was higher connectivity between MTG and STG for sentences compared to word lists at low accuracies. At high accuracies, we found that stronger MTG tracking at phrasal rates (measured with MI) for sentences compared to word lists during the word combination task. These results suggest that indeed tracking of phrasal structure in MTG is relevant to understand sentences compared to word lists. This was reflected in a general increase in delta connectivity differences when the task was difficult (Figure 7B). Participants might compensate for the difficulty using phrasal structure present in the sentence condition. When phrasal structure in sentences are accurately tracked (as measured with MI) performance is better when these rates are relevant (Figure 7A). These results point to a role for phrasal tracking for accurately understanding the higher order linguistic structure in sentences even though more research is needed to verify this. It is evident that the connectivity and tracking correlations to behaviour do not explain all variation in the behavioural performance (compare Figure 1 with 3). Plainly, temporal tracking does not explain everything in language processing. Besides tracking there are many other components important for our designated tasks, such as memory load and semantic context which are not captured by our current analyses.”

Author Response:

Reviewer #1 (Public Review):

[...] While the study is addressing an interesting topic, I also felt this manuscript was limited in novel findings to take away. Certainly the study clearly shows that substitution saturation is achieved at synonymous CpG sites. However, subsequent main analyses do not really show anything new: the depletion of segregating sites in functional versus neutral categories (Fig 2) has been extensively shown in the literature and polymorphism saturation is not a necessary condition for observing this pattern.

We agree with the reviewer that many of the points raised were appreciated previously and did not mean to convey another impression. Our aim was instead to highlight some unique opportunities provided by being at or very near saturation for mCpG transitions. In that regard, we note that although depletion of variation in functional categories is to be expected at any sample size, the selection strength that this depletion reflects is very different in samples that are far from saturated, where invariant sites span the entire spectrum from neutral to lethal. Consider the depletion per functional category relative to synonymous sites in the adjoining plot in a sample of 100k: ~40% of mCpG LOF sites do not have T mutations. From our Fig. 4 and b, it can be seen that these sites are associated with a much broader range of hs values than sites invariant at 780k, so that information about selection at an individual site is quite limited (indeed, in our p-value formulation, these sites would be assigned p≤0.35, see Fig. 1). Thus, only now can we really start to tease apart weakly deleterious mutations from strongly deleterious or even embryonic lethal mutations. This allows us to identify individual sites that are most likely to underlie pathogenic mutations and functional categories that harbor deleterious variation at the extreme end of the spectrum of possible selection coefficients. More generally, saturation is useful because it allows one to learn about selection with many fewer untested assumptions than previously feasible.

Similarly, the diminishing returns on sampling new variable sites has been shown in previous studies, for example the first "large" human datasets ca. 2012 (e.g. Fig 2 in Nelson et al. 2012, Science) have similar depictions as Figure 3B although with smaller sample sizes and different approaches (projection vs simulation in this study).

We agree completely: diminishing returns is expected on first principles from coalescent theory, which is why we cited a classic theory paper when making that point in the previous version of the manuscript. Nonetheless, the degree of saturation is an empirical question, since it depends on the unknown underlying demography of the recent past. In that regard, we note that Nelson et al. predict that at sample sizes of 400K chromosomes in Europeans, approximately 20% of all synonymous sites will be segregating at least one of three possible alleles, when the observed number is 29%. Regardless, not citing Nelson et al. 2012 was a clear oversight on our part, for which we apologize; we now cite it in that context and in mentioning the multiple merger coalescent.

There are some simulations presented in Fig 4, but this is more of a hypothetical representation of the site-specific DFE under simulation conditions roughly approximating human demography than formal inference on single sites. Again, these all describe the state of the field quite well, but I was disappointed by the lack of a novel finding derived from exploiting the mutation saturation properties at methylated CpG sites.

As noted above, in our view, the novelty of our results lies in their leveraging saturation in order to identify sites under extremely strong selection and make inferences about selection without the need to rely on strong, untested assumptions.

However, we note that Fig 4 is not simply a hypothetical representation, in that it shows the inferred DFE for single mCpG sites for a fixed mutation rate and given a plausible demographic model, given data summarized in terms of three ranges of allele frequency (i.e., = 0, between 1 and 10 copies, or above 10 copies). One could estimate a DFE across all sites from those summaries of the data (i.e., from the proportion of mCpG sites in each of the three frequency categories), by weighting the three densities in Fig 4 by those proportions. That is, in fact, what is done in a recent preprint by Dukler et al. (2021, BioRxiv): they infer the DFE from two summaries of the allele frequency spectrum (in bins of sites), the proportion of invariant sites and the proportion of alleles at 1-70 copies, in a sample of 70K chromosomes.

To illustrate how something similar could be done with Fig. 4 based on individual sites, we obtain an estimate of the DFE for LOF mutations (shown in Panel B and D for two different prior distributions on hs) by weighting the posterior densities in Panel A by the fraction of LOF mutations that are segregating (73% at 780K; 9% at 15K) and invariant (27% and 91% respectively); in panel C, we show the same for a different choice of prior. For the smaller sample size considered, the posterior distribution recapitulates the prior, because there is little information about selection in whether a site is observed to be segregating or invariant, and particularly about strong selection. In the sample of 780K, there is much more information about selection in a site being invariant and therefore, there is a shift towards stronger selection coefficients for LOF mutations regardless of the prior.

Our goal was to highlight these points rather than infer a DFE using these two summaries, which throw out much of the information in the data (i.e., the allele frequency differences among segregating sites). In that regard, we note that the DFE inference would be improved by using the allele frequency at each of 1.1 million individual mCpG sites in the exome. We outline this next step in the Discussion but believe it is beyond the scope of our paper, as it is a project in itself – in particular it would require careful attention to robustness with regard to both the demographic model (and its impact on multiple hits), biased gene conversion and variability in mutation rates among mCpG sites. We now make these points explicitly in the Outlook.

Similarly, I felt the authors posed a very important point about limitations of DFE inference methods in the Introduction but ended up not really providing any new insights into this problem. The authors argue (rightly so) that currently available DFE estimates are limited by both the sparsity of polymorphisms and limited flexibility in parametric forms of the DFE. However, the nonsynonymous human DFE estimates in the literature appear to be surprisingly robust to sample size: older estimates (Eyre-Walker et al. 2006 Genetics, Boyko et al. 2008 PLOS Genetics) seem to at least be somewhat consistent with newer estimates (assuming the same mutation rate) from samples that are orders of magnitude larger (Kim et al. 2017 Genetics).

We are not quite sure what the reviewer has in mind by “somewhat consistent,” as Boyko et al. estimate that 35% of non-synonymous mutations have s>10^-2 while Kim et al. find that proportion to be “0.38–0.84 fold lower” than the Boyko et al. estimate (see, e.g., Fig. 4 in Kim et al., 2017). Moreover, the preprint by Dukler et al. mentioned above, which infers the DFE based on ~70K chromosomes, finds estimates inconsistent with those of Kim et al. (see SOM Table 2 and SOM Figure S5 in Dukler et al., 2021).

More generally, given that even 70K chromosomes carry little information about much of the distribution of selection coefficients (see our Fig. 4), we expect that studies based on relatively sample sizes will basically recover something close to their prior; therefore, they should agree when they use the same or similar parametric forms for the distribution of selection coefficients and disagree otherwise. The dependence on that choice is nicely illustrated in Kim et al., who consider different choices and then perform inference on the same data set and with the same fixed mutation rate for exomes; depending on their choice anywhere between 5%-28% of non-synonymous changes are inferred to be under strong selection with s>=10^-2 (see their Table S4).

Whether a DFE inferred under polymorphism saturation conditions with different methods is different, and how it is different, is an issue of broad and immediate relevance to all those conducting population genomic simulations involving purifying selection. The analyses presented as Fig 4A and 4B kind of show this, but they are more a demonstration of what information one might have at 1M+ sample sizes rather than an analysis of whether genome-wide nonsynonymous DFE estimates are accurate. In other words, this manuscript makes it clear that a problem exists, that it is a fundamental and important problem in population genetics, and that with modern datasets we are now poised to start addressing this problem with some types of sites, but all of this is already very well-appreciated except for perhaps the last point.

At least a crude analysis to directly compare the nonsynonymous genome-wide DFE from smaller samples to the 780K sample would be helpful, but it should be noted that these kinds of analyses could be well beyond the scope of the current manuscript. For example, if methylated nonsynonymous CpG sites are under a different level of constraint than other nonsynonymous sites (Fig. S14) then comparing results to a genome-wide nonsynonymous DFE might not make sense and any new analysis would have to try and infer a DFE independently from synonymous/nonsynonymous methylated CpG sites.

We are not sure what would be learned from this comparison, given that Figure 4 shows that, at least with an uninformative prior, there is little information about the true DFE in samples, even of tens of thousands of individuals. Thus, if some of the genome-wide nonsynonymous DFE estimates based on small sample sizes turn out to be accurate, it will be because the guess about the parametric shape of the DFE was an inspired one. In our view, that is certainly possible but not likely, given that the shape of the DFE is precisely what the field has been aiming to learn and, we would argue, what we are now finally in a position to do for CpG mutations in humans.

Reviewer #2 (Public Review):

This manuscript presents a simple and elegant argument that neutrally evolving CpG sites are now mutationally saturated, with each having a 99% probability of containing variation in modern datasets containing hundreds of thousands of exomes. The authors make a compelling argument that for CpG sites where mutations would create genic stop codons or impair DNA binding, about 20% of such mutations are strongly deleterious (likely impairing fitness by 5% or more). Although it is not especially novel to make such statements about the selective constraint acting on large classes of sites, the more novel aspect of this work is the strong site-by-site prediction it makes that most individual sites without variation in UK Biobank are likely to be under strong selection.

The authors rightly point out that since 99% of neutrally evolving CpG sites contain variation in the data they are looking at, a CpG site without variation is likely evolving under constraint with a p value significance of 0.01. However, a weakness of their argument is that they do not discuss the associated multiple testing problem-in other words, how likely is it that a given non synonymous CpG site is devoid of variation but actually not under strong selection? Since one of the most novel and useful deliverables of this paper is single-base-pair-resolution predictions about which sites are under selection, such a multiple testing correction would provide important "error bars" for evaluating how likely it is that an individual CpG site is actually constrained, not just the proportion of constrained sites within a particular functional category.

We thank the reviewer for pointing this out. One way to think about this problem might be in terms of false discovery rates, in which case the FDR would be 16% across all non-synonymous mCpG sites that are invariant in current samples, and ~4% for the subset of those sites where mutations lead to loss-of-function of genes.

Another way to address this issue, which we had included but not emphasized previously, is by examining how one’s beliefs about selection should be updated after observing a site to be invariant (i.e., using Bayes odds). At current sample sizes and assuming our uninformative prior, for a non-synonymous mCpG site that does not have a C>T mutation, the Bayes odds are 15:1 in favor of hs>0.5x10^-3; thus the chance that such a site is not under strong selection is 1/16, given our prior and demographic model. These two approaches (FDR and Bayes odds) are based on somewhat distinct assumptions.

We have now added and/or emphasized these two points in the main text.

The paper provides a comparison of their functional predictions to CADD scores, an older machine-learning-based attempt at identifying site by site constraint at single base pair resolution. While this section is useful and informative, I would have liked to see a discussion of the degree to which the comparison might be circular due to CADD's reliance on information about which sites are and are not variable. I had trouble assessing this for myself given that CADD appears to have used genetic variation data available a few years ago, but obviously did not use the biobank scale datasets that were not available when that work was published.

We apologize for the lack of clarity in the presentation. We meant to emphasize that de novo mutation rates vary across CADD deciles when considering all CpG sites (Fig. 2-figure supplement 5c), which confounds CADD precisely because it is based in part on which sites are variable. We have edited the manuscript to clarify this.

Reading this paper left me excited about the possibility of examining individual invariant CpG sites and deducing how many of them are already associated with known disease phenotypes. I believe the paper does not mention how many of these invariant sites appear in Clinvar or in databases of patients with known developmental disorders, and I wondered how close to saturation disease gene databases might be given that individuals with developmental disorders are much more likely to have their exomes sequenced compared to healthy individuals. One could imagine some such analyses being relatively low hanging fruit that could strengthen the current paper, but the authors also make several reference to a companion paper in preparation that deals more directly with the problem of assessing clinical variant significance. This is a reasonable strategy, but it does give the discussion section of the paper somewhat of a "to be continued" feel.

We apologize for the confusion that arose from our references to a second manuscript in prep. The companion paper is not a continuation of the current manuscript: it contains an analysis of fitness and pathogenic effects of loss-of-function variation in human exomes.

Following the reviewer’s suggestion to address the clinical significance of our results, we have now examined the relationship of mCpG sites invariant in current samples with Clinvar variants. We find that of the approximately 59,000 non-synonymous mCpG sites that are invariant, only ~3.6% overlap with C>T variants associated with at least one disease and classified as likely pathogenic in Clinvar (~5.8% if we include those classified as uncertain or with conflicting evidence as pathogenic). Approximately 2% of invariant mCpGs have C>T mutations in what is, to our knowledge, the largest collection of de novo variants ascertained in ~35,000 individuals with developmental disorders (DDD, Kaplanis et al. 2020). At the level of genes, of the 10k genes that have at least one invariant non-synonymous mCpG, only 8% (11% including uncertain variants) have any non-synonymous hits in Clinvar, and ~8% in DDD. We think it highly unlikely that the large number of remaining invariant sites are not seen with mutations in these databases because such mutations are lethal; rather it seems to us to be the case that these disease databases are far from saturation as they contain variants from a relatively small number of individuals, are subject to various ascertainment biases both at the variant level and at the individual level, and only contain data for a small subset of existing severe diseases.

With a view to assessing clinical relevance however, we can ask a related question, namely how informative being invariant in a sample of 780k is about pathogenicity in Clinvar. Although the relationship between selection and pathogenicity is far from straightforward, being an invariant non-synonymous mCpG in current samples not only substantially increases (15-10fold) the odds of hs > 0.5x10-3 (see Fig. 4b), it also increases the odds of being classified as pathogenic vs. benign in Clinvar 8-51 fold. In the DDD sample, we don’t know which variants are pathogenic; however, if we consider non-synonymous mutations that occur in consensus DDD genes as pathogenic (a standard diagnostic criterion), being invariant increases the odds of being classified as pathogenic 6-fold. We caution that both Clinvar classifications and the identification of consensus genes in DDD relies in part on whether a site is segregating in datasets like ExAC, so this exercise is somewhat circular. Nonetheless it illustrates that there is some information about clinical importance in mCpG sites that are invariant in current samples, and that the degree of enrichment (6 to 51-fold) is very roughly on par with the Bayes odds that we estimate of strong selection conditional on a site being invariant. We have added these findings to the main text and added the plot as Supplementary Figure 13.

Reviewer #3 (Public Review):

[...] The authors emphasize several times how important an accurate demographic model is. While we may be close to a solid demographic model for humans, this is certainly not the case for many other organisms. Yet we are not far off from sufficient sample sizes in a number of species to begin to reach saturation. I found myself wondering how different the results/inference would be under a different model of human demographic history. Though likely the results would be supplemental, it would be nice in the main text to be able to say something about whether results are qualitatively different under a somewhat different published model.

We had previously examined the effect of a few demographic scenarios with large increases in population size towards the present on the average length of the genealogy of a sample (and hence the expected number of mutations at a site) in Figure 3-figure supplement 1b, but without quantifying the effect on our selection inference. Following this suggestion, we now consider a widely used model of human demography inferred from a relatively small sample, and therefore not powered to detect the huge increase in population size towards the present (Tennessen et al. 2012). Using this model, we find a poor fit to the proportion of segregating CpG sites (the observed fraction is 99% in 780k exomes, when the model predicts 49%). Also, as expected, inferences about selection depend on the accuracy of the demographic model (as can be seen by comparing panel B to Fig 4B in the main text).

On a similar note, while a fixed hs simplifies much of the analysis, I wondered how results would differ for 1) completely recessive mutations and 2) under a distribution of dominance coefficients, especially one in which the most deleterious alleles were more recessive. Again, though I think it would strengthen the manuscript by no means do I feel this is a necessary addition, though some discussion of variation in dominance would be an easy and helpful add.

There's some discussion of population structure, but I also found myself wondering about GxE. That is, another reason a variant might be segregating is that it's conditionally neutral in some populations and only deleterious in a subset. I think no analysis to be done here, but perhaps some discussion?

We agree that our analysis ignores the possibilities of complete recessivity in fitness (h=0) as well as more complicated selection scenarios, such as spatially-varying selection (of the type that might be induced by GxE). We note however that so long as there are any fitness effects in heterozygotes, the allele dynamics will be primarily governed by hs; one might also imagine that under some conditions, the mean selection effect across environments would predict allele dynamics reasonably well even in the presence of GxE. Also worth exploring in our view is the standard assumption that hs remains fixed even as Ne changes dramatically. We now mention these points in the Outlook.

Maybe I missed it, but I don't think the acronym DNM is explained anywhere. While it was fairly self-explanatory, I did have a moment of wondering whether it was methylation or mutation and can't hurt to be explicit.

We apologize for the oversight and have updated the text accordingly.

Author Response

Reviewer #1 (Public Review):

The authors evaluate the involvement of the hippocampus in a fast-paced time-to-contact estimation task. They find that the hippocampus is sensitive to feedback received about accuracy on each trial and has activity that tracks behavioral improvement from trial to trial. Its activity is also related to a tendency for time estimation behavior to regress to the mean. This is a novel paradigm to explore hippocampal activity and the results are thus novel and important, but the framing as well as discussion about the meaning of the findings obscures the details of the results or stretches beyond them in many places, as detailed below.

We thank the reviewer for their constructive feedback and were happy to read that s/he considered our approach and results as novel and important. The comments led us to conduct new fMRI analyses, to clarify various unclear phrasings regarding our methods, and to carefully assess our framing of the interpretation and scope of our results. Please find our responses to the individual points below.

1) Some of the results appear in the posterior hippocampus and others in the anteriorhippocampus. The authors do not motivate predictions for anterior vs. posterior hippocampus, and they do not discuss differences found between these areas in the Discussion. The hippocampus is treated as a unitary structure carrying out learning and updating in this task, but the distinct areas involved motivate a more nuanced picture that acknowledges that the same populations of cells may not be carrying out the various discussed functions.

We thank the reviewer for pointing this out. We split the hippocampus into anterior and posterior sections because prior work suggested a different whole-brain connectivity and function of the two. This was mentioned in the methods section (page 15) in the initial submission but unfortunately not in the main text. Moreover, when discussing the results, we did indeed refer mostly to the hippocampus as a unitary structure for simplicity and readability, and because statements about subcomponents are true for the whole. However, we agree with the reviewer that the differences between anterior and posterior sections are very interesting, and that describing these effects in more detail might help to guide future work more precisely.

In response to the reviewer's comment, we therefore clarified at various locations throughout the manuscript whether the respective results were observed in the posterior or anterior section of the hippocampus, and we extended our discussion to reflect the idea that different functions may be carried out by distinct populations of hippocampal cells. In addition, we also now motivate the split into the different sections better in the main text. We made the following changes.

Page 3: “Second, we demonstrate that anterior hippocampal fMRI activity and functional connectivity tracks the behavioral feedback participants received in each trial, revealing a link between hippocampal processing and timing-task performance.

Page 3: “Fourth, we show that these updating signals in the posterior hippocampus were independent of the specific interval that was tested and activity in the anterior hippocampus reflected the magnitude of the behavioral regression effect in each trial.”

Page 5: “We performed both whole-brain voxel-wise analyses as well as regions-of-interest (ROI) analysis for anterior and posterior hippocampus separately, for which prior work suggested functional differences with respect to their contributions to memory-guided behavior (Poppenk et al., 2013, Strange et al. 2014).”

Page 9: “Because anterior and posterior sections of the hippocampus differ in whole-brain connectivity as well as in their contributions to memory-guided behavior (Strange et al. 2014), we analyzed the two sections separately. “

Page 9: “We found that anterior hippocampal activity as well as functional connectivity reflected the feedback participants received during this task, and its activity followed the performance improvements in a temporal-context-dependent manner. Its activity reflected trial-wise behavioral biases towards the mean of the sampled intervals, and activity in the posterior hippocampus signaled sensorimotor updating independent of the specific intervals tested.”

Page 10: “Intriguingly, the mechanisms at play may build on similar temporal coding principles as those discussed for motor timing (Yin & Troger, 2011; Eichenbaum, 2014; Howard, 2017; Palombo & Verfaellie, 2017; Nobre & van Ede, 2018; Paton & Buonomano, 2018; Bellmund et al., 2020, 2021; Shikano et al., 2021; Shimbo et al., 2021), with differential contributions of the anterior and posterior hippocampus. Note that our observation of distinct activity modulations in the anterior and posterior hippocampus suggests that the functions and coding principles discussed here may be mediated by at least partially distinct populations of hippocampal cells.”

Page 11: Interestingly, we observed that functional connectivity of the anterior hippocampus scaled negatively (Fig. 2C) with feedback valence [...]

2) Hippocampal activity is stronger for smaller errors, which makes the interpretationmore complex than the authors acknowledge. If the hippocampus is updating sensorimotor representations, why would its activity be lower when more updating is needed?

Indeed, we found that absolute (univariate) activity of the hippocampus scaled with feedback valence, the inverse of error (Fig. 2A). We see multiple possibilities for why this might be the case, and we discussed some of them in a dedicated discussion section (“The role of feedback in timed motor actions”). For example, prior work showed that hippocampal activity reflects behavioral feedback also in other tasks, which has been linked to learning (e.g. Schönberg et al., 2007; Cohen & Ranganath, 2007; Shohamy & Wagner, 2008; Foerde & Shohamy, 2011; Wimmer et al., 2012). In our understanding, sensorimotor updating is a form of ‘learning’ in an immediate and behaviorally adaptive manner, and we therefore consider our results well consistent with this earlier work. We agree with the reviewer that in principle activity should be stronger if there was stronger sensorimotor updating, but we acknowledge that this intuition builds on an assumption about the relationship between hippocampal neural activity and the BOLD signal, which is not entirely clear. For example, prior work revealed spatially informative negative BOLD responses in the hippocampus as a function of visual stimulation (e.g. Szinte & Knapen 2020), and the effects of inhibitory activity - a leading motif in the hippocampal circuitry - on fMRI data are not fully understood. This raises the possibility that the feedback modulation we observed might also involve negative BOLD responses, which would then translate to the observed negative correlation between feedback valence and the hippocampal fMRI signal, even if the magnitude of the underlying updating mechanism was positively correlated with error. This complicates the interpretation of the direction of the effect, which is why we chose to avoid making strong conclusions about it in our manuscript. Instead, we tried discussing our results in a way that was agnostic to the direction of the feedback modulation. Importantly, hippocampal connectivity with other regions did scale positively with error (Fig. 2B), which we again discussed in the dedicated discussion section.

In response to the reviewer’s comment, we revisited this section of our manuscript and felt the latter result deserved a better discussion. We therefore took this opportunity to extend our discussion of the connectivity results (including their relationship to the univariate-activity results as well as the direction of these effects), all while still avoiding strong conclusions about directionality. Following changes were made to the manuscript.

Page 11: Interestingly, we observed that functional connectivity of the anterior hippocampus scaled negatively (Fig. 2C) with feedback valence, unlike its absolute activity, which scaled positively with feedback valence (Fig. 2A,B), suggesting that the two measures may be sensitive to related but distinct processes.

Page 11: Such network-wide receptive-field re-scaling likely builds on a re-weighting of functional connections between neurons and regions, which may explain why anterior hippocampal connectivity correlated negatively with feedback valence in our data. Larger errors may have led to stronger re-scaling, which may be grounded in a corresponding change in functional connectivity.

3) Some tests were one-tailed without justification, which reduces confidence in the robustness of the results.

We thank the reviewer for pointing us to the fact that our choice of statistical tests was not always clear in the manuscript. In the analysis the reviewer is referring to, we predicted that stronger sensorimotor updating should lead to stronger activity as well as larger behavioral improvements across the respective trials. This is because a stronger update should translate to a more accurate “internal model” of the task and therefore to a better performance. We tested this one-sided hypothesis using the appropriate test statistic (contrasting trials in which behavioral performance did improve versus trials in which it did not improve), but we did not motivate our reasoning well enough in the manuscript. The revised manuscript therefore includes the two new statements shown below to motivate our choice of test statistic more clearly.

Page 7: [...] we contrasted trials in which participants had improved versus the ones in which they had not improved or got worse (see methods for details). Because stronger sensorimotor updating should lead to larger performance improvements, we predicted to find stronger activity for improvements vs. no improvements in these tests (one-tailed hypothesis).

Page 18: These two regressors reflect the tests for target-TTC-independent and target-TTC-specific updating, respectively. Because we predicted to find stronger activity for improvements vs. no improvements in behavioral performance, we here performed one-tailed statistical tests, consistent with the direction of this hypothesis. Improvement in performance was defined as receiving feedback of higher valence than in the corresponding previous trial.

4) The introduction motivates the novelty of this study based on the idea that thehippocampus has traditionally been thought to be involved in memory at the scale of days and weeks. However, as is partially acknowledged later in the Discussion, there is an enormous literature on hippocampal involvement in memory at a much shorter timescale (on the order of seconds). The novelty of this study is not in the timescale as much as in the sensorimotor nature of the task.

We thank the reviewer for this helpful suggestion. We agree that a key part of the novelty of this study is the use of the task that is typically used to study sensorimotor integration and timing rather than hippocampal processing, along with the new insights this task enabled about the role of the hippocampus in sensorimotor updating. As mentioned in the discussion, we also agree with the reviewer that there is prior literature linking hippocampal activity to mnemonic processing on short time scales. We therefore rephrased the corresponding section in the introduction to put more weight on the sensorimotor nature of our task instead of the time scales.

Note that the new statement still includes the time scale of the effects, but that it is less at the center of the argument anymore. We chose to keep it in because we do think that the majority of studies on hippocampal-dependent memory functions focus on longer time scales than our study does, and we expect that many readers will be surprised about the immediacy of how hippocampal activity relates to ongoing behavioral performance (on ultrashort time scales).

We changed the introduction to the following.

Page 2: Here, we approach this question with a new perspective by converging two parallel lines of research centered on sensorimotor timing and hippocampal-dependent cognitive mapping. Specifically, we test how the human hippocampus, an area often implicated in episodic-memory formation (Schiller et al., 2015; Eichenbaum, 2017), may support the flexible updating of sensorimotor representations in real time and in concert with other regions. Importantly, the hippocampus is not traditionally thought to support sensorimotor functions, and its contributions to memory formation are typically discussed for longer time scales (hours, days, weeks). Here, however, we characterize in detail the relationship between hippocampal activity and real-time behavioral performance in a fast-paced timing task, which is traditionally believed to be hippocampal-independent. We propose that the capacity of the hippocampus to encode statistical regularities of our environment (Doeller et al. 2005, Shapiro et al. 2017, Behrens et al., 2018; Momennejad, 2020; Whittington et al., 2020) situates it at the core of a brain-wide network balancing specificity vs. regularization in real time as the relevant behavior is performed.

5) The authors used three different regressors for the three feedback levels, asopposed to a parametric regressor indexing the level of feedback. The predictions are parametric, so a parametric regressor would be a better match, and would allow for the use of all the medium-accuracy data.

The reviewer raises a good point that overlaps with question 3 by reviewer 2. In the current analysis, we model the three feedback levels with three independent regressors (high, medium, low accuracy). We then contrast high vs. low accuracy feedback, obtaining the results shown in Fig. 2AB. The beta estimates obtained for medium-accuracy feedback are being ignored in this contrast. Following the reviewer’s feedback, we therefore re-run the model, this time modeling all three feedback levels in one parametric regressor. All other regressors in the model stayed the same. Instead of contrasting high vs. low accuracy feedback, we then performed voxel-wise t-tests on the beta estimates obtained for the parametric feedback regressor.

The results we observed were highly consistent across the two analyses, and all conclusions presented in the initial manuscript remain unchanged. While the exact t-scores differ slightly, we replicated the effects for all clusters on the voxel-wise map (on whole-brain FWE-corrected levels) as well as for the regions-of-interest analysis for anterior and posterior hippocampus. These results are presented in a new Supplementary Figure 3C.

Note that the new Supplementary Figure 3B shows another related new analyses we conducted in response to question 4 of reviewer 2. Here, we re-ran the initial analysis with three feedback regressors, but without modeling the inter-trial interval (ITI) and the inter-session interval (ISI, i.e. the breaks participants took) to avoid model over-specification. Again, we replicated the results for all clusters and the ROI analysis, showing that the initial results we presented are robust.

The following additions were made to the manuscript.

Page 5: Note that these results were robust even when fewer nuisance regressors were included to control for model over-specification (Fig. S3B; two-tailed one-sample t tests: anterior HPC, t(33) = -3.65, p = 8.9x10-4, pfwe = 0.002, d=-0.63, CI: [-1.01, -0.26]; posterior HPC, t(33) = -1.43, p = 0.161, pfwe = 0.322, d=-0.25, CI: [-0.59, 0.10]), and when all three feedback levels were modeled with one parametric regressors (Fig. S3C; two-tailed one-sample t tests: anterior HPC, t(33) = -3.59, p = 0.002, pfwe = 0.005, d=-0.56, CI: [-0.93, -0.20]; posterior HPC, t(33) = -0.99, p = 0.329, pfwe = 0.659, d=-0.17, CI: [-0.51, 0.17]). Further, there was no systematic relationship between subsequent trials on a behavioral level [...]

Page 17: Moreover, instead of modeling the three feedback levels with three independent regressors, we repeated the analysis modeling the three feedback levels as one parametric regressor with three levels. All other regressors remained unchanged, and the model included the regressors for ITIs and ISIs. We then conducted t-tests implemented in SPM12 using the beta estimates obtained for the parametric feedback regressor (Fig. 2C). Compared to the initial analyses presented above, this has the advantage that medium-accuracy feedback trials are considered for the statistics as well.

6) The authors claim that the results support the idea that the hippocampus is findingan "optimal trade-off between specificity and regularization". This seems overly speculative given the results presented.

We understand the reviewer's skepticism about this statement and agree that the manuscript does not show that the hippocampus is finding the trade-off between specificity and regularization. However, this is also not exactly what the manuscript claims. Instead, it suggests that the hippocampus “may contribute” to solving this trade-off (page 3) as part of a “brain-wide network“ (pages 2,3,9,12). We also state that “Our [...] results suggest that this trade-off [...] is governed by many regions, updating different types of task information in parallel” (Page 11). To us, these phrasings are not equivalent, because we do not think that the role of the hippocampus in sensorimotor updating (or in any process really) can be understood independently from the rest of the brain. We do however think that our results are in line with the idea that the hippocampus contributes to solving this trade-off, and that this is exciting and surprising given the sensorimotor nature of our task, the ultrashort time scale of the underlying process, and the relationship to behavioral performance. We tried expressing that some of the points discussed remain speculation, but it seems that we were not always successful in doing so in the initial submission. We apologize for the misunderstanding, adapted corresponding statements in the manuscript, and we express even more carefully that these ideas are speculation.

Following changes were made to the introduction and discussion.

Page 2: Here, we approach this question with a new perspective by converging two parallel lines of research centered on sensorimotor timing and hippocampal-dependent cognitive mapping. Specifically, we test how the human hippocampus, an area often implicated in episodic-memory formation (Schiller et al., 2015; Eichenbaum, 2017), may support the flexible updating of sensorimotor representations in real time and in concert with other regions.

Page 12: Because hippocampal activity (Julian & Doeller, 2020) and the regression effect (Jazayeri & Shadlen, 2010) were previously linked to the encoding of (temporal) context, we reasoned that hippocampal activity should also be related to the regression effect directly. This may explain why hippocampal activity reflected the magnitude of the regression effect as well as behavioral improvements independently from TTC, and why it reflected feedback, which informed the updating of the internal prior.

Page 12: This is in line with our behavioral results, showing that TTC-task performance became more optimal in the face of both of these two objectives. Over time, behavioral responses clustered more closely between the diagonal and the average line in the behavioral response profile (Fig. 1B, S1G), and the TTC error decreased over time. While different participants approached these optimal performance levels from different directions, either starting with good performance or strong regularization, the group approached overall optimal performance levels over the course of the experiment.

Page 13: This is in line with the notion that the hippocampus [...] supports finding an optimal trade off between specificity and regularization along with other regions. [...] Our results show that the hippocampus supports rapid and feedback-dependent updating of sensorimotor representations, suggesting that it is a central component of a brain-wide network balancing task specificity vs. regularization for flexible behavior in humans.

Note that in response to comment 1 by reviewer 2, the revised manuscript now reports the results of additional behavioral analyses that support the notion that participants find an optimal trade-off between specificity and regularization over time (independent of whether the hippocampus was involved or not).

7) The authors find that hippocampal activity is related to behavioral improvement fromthe prior trial. This seems to be a simple learning effect (participants can learn plenty about this task from a prior trial that does not have the exact same timing as the current trial) but is interpreted as sensitivity to temporal context. The temporal context framing seems too far removed from the analyses performed.

We agree with the reviewer that our observation that hippocampal activity reflects TTC-independent behavioral improvements across trials could have multiple explanations. Critically, i) one of them is that the hippocampus encodes temporal context, ii) it is only one of multiple observations that we build our interpretation on, and iii) our interpretation builds on multiple earlier reports

Interval estimates regress toward the mean of the sampled intervals, an effect that is often referred to as the “regression effect”. This effect, which we observed in our data too (Fig. 1B), has been proposed to reflect the encoding of temporal context (e.g. Jazayeri & Shadlen 2010). Moreover, there is a large body of literature on how the hippocampus may support the encoding of spatial and temporal context (e.g. see Bellmund, Polti & Doeller 2020 for review).

Because both hippocampal activity and the regression effect were linked to the encoding of (temporal) context, we reasoned that hippocampal activity should also be related to the regression effect directly. If so, one would expect that hippocampal activity should reflect behavioral improvements independently from TTC, it should reflect the magnitude of the regression effect, and it should generally reflect feedback, because it is the feedback that informs the updating of the internal prior.

All three observations may have independent explanations indeed, but they are all also in line with the idea that the hippocampus does encode temporal context and that this explains the relationship between hippocampal activity and the regression effect. It therefore reflects a sparse and reasonable explanation in our opinion, even though it necessarily remains an interpretation. Of course, we want to be clear on what our results are and what our interpretations are.

In response to the reviewer’s comment, we therefore toned down two of the statements that mention temporal context in the manuscript, and we removed an overly speculative statement from the result section. In addition, the discussion now describes more clearly how our results are in line with this interpretation.

Abstract: This is in line with the idea that the hippocampus supports the rapid encoding of temporal context even on short time scales in a behavior-dependent manner.

Page 13: This is in line with the notion that the hippocampus encodes temporal context in a behavior-dependent manner, and that it supports finding an optimal trade off between specificity and regularization along with other regions.

Page 12: Because hippocampal activity (Julian & Doeller, 2020) and the regression effect (Jazayeri & Shadlen, 2010) were previously linked to the encoding of (temporal) context, we reasoned that hippocampal activity should also be related to the regression effect directly. This may explain why hippocampal activity reflected the magnitude of the regression effect as well as behavioral improvements independently from TTC, and why it reflected feedback, which informed the updating of the internal prior.

The following statement was removed, overlapping with comment 2 by Reviewer 3:

Instead, these results are consistent with the notion that hippocampal activity signals the updating of task-relevant sensorimotor representations in real-time.

8) I am not sure the term "extraction of statistical regularities" is appropriate. The termis typically used for more complex forms of statistical relationships.

We agree with the reviewer that this expression may be interpreted differently by different readers and are grateful to be pointed to this fact. We therefore removed it and instead added the following (hopefully less ambiguous) statement to the manuscript.

Page 9: This study investigated how the human brain flexibly updates sensorimotor representations in a feedback-dependent manner in the service of timing behavior.

Reviewer #2 (Public Review):

The authors conducted a study involving functional magnetic resonance imaging and a time-to-contact estimation paradigm to investigate the contribution of the human hippocampus (HPC) to sensorimotor timing, with a particular focus on the involvement of this structure in specific vs. generalized learning. Suggestive of the former, it was found that HPC activity reflected time interval-specific improvements in performance while in support of the latter, HPC activity was also found to signal improvements in performance, which were not specific to the individual time intervals tested. Based on these findings, the authors suggest that the human HPC plays a key role in the statistical learning of temporal information as required in sensorimotor behaviour.

By considering two established functions of the HPC (i.e., temporal memory and generalization) in the context of a domain that is not typically associated with this structure (i.e., sensorimotor timing), this study is potentially important, offering novel insight into the involvement of the HPC in everyday behaviour. There is much to like about this submission: the manuscript is clearly written and well-crafted, the paradigm and analyses are well thought out and creative, the methodology is generally sound, and the reported findings push us to consider HPC function from a fresh perspective. A relative weakness of the paper is that it is not entirely clear to what extent the data, at least as currently reported, reflects the involvement of the HPC in specific and generalized learning. Since the authors' conclusions centre around this observation, clarifying this issue is, in my opinion, of primary importance.

We thank the reviewer for these positive and extremely helpful comments, which we will address in detail below. In response to these comments, the revised manuscript clarifies why the observed performance improvements are not at odds with the idea that an optimal trade-off between specificity and regularization is found, and how the time course of learning relates to those reported in previous literature. In addition, we conducted two new fMRI analyses, ensuring that our conclusions remain unchanged even if feedback is modeled with one parametric regressor, and if the number or nuisance regressors is reduced to control for overparameterization of the model. Please find our responses underneath each individual point below.

1) Throughout the manuscript, the authors discuss the trade-off between specific and generalized learning, and point towards Figure S1D as evidence for this (i.e., participants with higher TTC accuracy exhibited a weaker regression effect). What appears to be slightly at odds with this, however, is the observation that the deviation from true TTC decreased with time (Fig S1F) as the regression line slope approached 0.5 (Fig S1E) - one would have perhaps expected the opposite i.e., for deviation from true TTC to increase as generalization increases. To gain further insight into this, it would be helpful to see the deviation from true TTC plotted for each of the four TTC intervals separately and as a signed percentage of the target TTC interval (i.e., (+) or (-) deviation) rather than the absolute value.

We thank the reviewer for raising this important question and for the opportunity to elaborate on the relationship between the TTC error and the magnitude of the regression effect in behavior. Indeed, we see that the regression slopes approach 0.5 and that the TTC error decreases over the course of the experiment. We do not think that these two observations are at odds with each other for the following reasons:

First, while the reviewer is correct in pointing out that the deviation from the TTC should increase as “generalization increases”, that is not what we found. It was not the magnitude of the regularization per se that increased over time, but the overall task performance became more optimal in the face of both objectives: specificity and generalization. This optimum is at a regression-line slope of 0.5. Generalization (or regularization how we refer to it in the present manuscript), therefore did not increase per se on group level.

Second, the regression slopes approached 0.5 on the group-level, but the individual participants approached this level from different directions: Some of them started with a slope value close to 1 (high accuracy), whereas others started with a slope value close to 0 (near full regression to the mean). Irrespective of which slope value they started with, over time, they got closer to 0.5 (Rebuttal Figure 1A). This can also be seen in the fact that the group-level standard deviation in regression slopes becomes smaller over the course of the experiment (Rebuttal Figure 1B, SFig 1G). It is therefore not generally the case that the regression effect becomes stronger over time, but that it becomes more optimal for longer-term behavioral performance, which is then also reflected in an overall decrease in TTC error. Please see our response to the reviewer’s second comment for more discussion on this.

Third, the development of task performance is a function of two behavioral factors: a) the accuracy and b) the precision in TTC estimation. Accuracy describes how similar the participant’s TTC estimates were to the true TTC, whereas precision describes how similar the participant’s TTC estimates were relative to each other (across trials). Our results are a reflection of the fact that participants became both more accurate over time on average, but also more precise. To demonstrate this point visually, we now plotted the Precision and the Accuracy for the 8 task segments below (Rebuttal Figure 1C, SFig 1H), showing that both measures increased as the time progressed and more trials were performed. This was the case for all target durations.

In response to the reviewer’s comment, we clarified in the main text that these findings are not at odds with each other. Furthermore, we made clear that regularization per se did not increase over time on group level. We added additional supporting figures to the supplementary material to make this point. Note that in our view, these new analyses and changes more directly address the overall question the reviewer raised than the figure that was suggested, which is why we prioritized those in the manuscript.

However, we appreciated the suggestion a lot and added the corresponding figure for the sake of completeness.

Following additions were made.

Page 5: In support of this, participants' regression slopes converged over time towards the optimal value of 0.5, i.e. the slope value between veridical performance and the grand mean (Fig. S1F; linear mixed-effects model with task segment as a predictor and participants as the error term, F(1) = 8.172, p = 0.005, ε2=0.08, CI: [0.01, 0.18]), and participants' slope values became more similar (Fig. S1G; linear regression with task segment as predictor, F(1) = 6.283, p = 0.046, ε2 = 0.43, CI: [0, 1]). Consequently, this also led to an improvement in task performance over time on group level (i.e. task accuracy and precision increased (Fig. S1I), and the relationship between accuracy and precision became stronger (Fig. S1H), linear mixed-effect model results for accuracy: F(1) = 15.127, p = 1.3x10-4, ε2=0.06, CI: [0.02, 0.11], precision: F(1) = 20.189, p = 6.1x10-5, ε2 = 0.32, CI: [0.13, 1]), accuracy-precision relationship: F(1) = 8.288, p =0.036, ε2 = 0.56, CI: [0, 1], see methods for model details).

Page 12: This suggests that different regions encode distinct task regularities in parallel to form optimal sensorimotor representations to balance specificity and regularization. This is in line with our behavioral results, showing that TTC-task performance became more optimal in the face of both of these two objectives. Over time, behavioral responses clustered more closely between the diagonal and the average line in the behavioral response profile (Fig. 1B, S1G), and the TTC error decreased over time. While different participants approached these optimal performance levels from different directions, either starting with good performance or strong regularization, the group approached overall optimal performance levels over the course of the experiment.

Page 15: We also corroborated this effect by measuring the dispersion of slope values between participants across task segments using a linear regression model with task segment as a predictor and the standard deviation of slope values across participants as the dependent variable (Fig. S1G). As a measure of behavioral performance, we computed two variables for each target-TTC level: sensorimotor timing accuracy, defined as the absolute difference in estimated and true TTC, and sensorimotor timing precision, defined as coefficient of variation (standard deviation of estimated TTCs divided by the average estimated TTC). To study the interaction between these two variables for each target TTC over time, we first normalized accuracy by the average estimated TTC in order to make both variables comparable. We then used a linear mixed-effects model with precision as the dependent variable, task segment and normalized accuracy as predictors and target TTC as the error term. In addition, we tested whether accuracy and precision increased over the course of the experiment using separate linear mixed-effects models with task segment as predictor and participants as the error term.

2) Generalization relies on prior experience and can be relatively slow to develop as is the case with statistical learning. In Jazayeri and Shadlen (2010), for instance, learning a prior distribution of 11-time intervals demarcated by two briefly flashed cues (compared to 4 intervals associated with 24 possible movement trajectories in the current study) required ~500 trials. I find it somewhat surprising, therefore, that the regression line slope was already relatively close to 0.5 in the very first segment of the task. To what extent did the participants have exposure to the task and the target intervals prior to entering the scanner?

We thank the reviewer for raising the important question about the time course of learning in our task and how our results relate to prior work on this issue. Addressing the specific reviewer question first, participants practiced the task for 2-3 minutes prior to scanning. During the practice, they were not specifically instructed to perform the task as well as they could nor to encode the intervals, but rather to familiarize themselves with the general experimental setup and to ask potential questions outside the MRI machine. While they might have indeed started encoding the prior distribution of intervals during the practice already, we have no way of knowing, and we expect the contribution of this practice on the time course of learning during scanning to be negligible (for the reasons outlined above).

However, in addition to the specific question the reviewer asked, we feel that the comment raises two more general points: 1) How long does it take to learn the prior distribution of a set of intervals as a function of the number of intervals tested, and 2) Why are the learning slopes we report quite shallow already in the beginning of the scan?

Regarding (1), we are not aware of published reports that answer this question directly, and we expect that this will depend on the task that is used. Regarding the comparison to Jazayeri & Shadlen (2010), we believe the learning time course is difficult to compare between our study and theirs. As the reviewer mentioned, our study featured only 4 intervals compared to 11 in their work, based on which we would expect much faster learning in our task than in theirs. We did indeed sample 24 movement directions, but these were irrelevant in terms of learning the interval distribution. Moreover, unlike Jazayeri & Shadlen (2010), our task featured moving stimuli, which may have added additional sensory, motor and proprioceptive information in our study which the participants of the prior study could not rely on.

Regarding (2), and overlapping with the reviewer’s previous comment, the average learning slope in our study is indeed close to 0.5 already in the first task segment, but we would like to highlight that this is a group-level measure. The learning slopes of some subjects were closer to 1 (i.e. the diagonal in Fig 1B), and the one of others was closer to 0 (i.e. the mean) in the beginning of the experiment. The median slope was close to 0.65. Importantly, the slopes of most participants still approached 0.5 in the course of the experiment, and so did even the group-level slope the reviewer is referring to. This also means that participants’ slopes became more similar in the course of the experiment, and they approached 0.5, which we think reflects the optimal trade-off between regressing towards the mean and regressing towards the diagonal (in the data shown in Fig. 1B). This convergence onto the optimal trade-off value can be seen in many measures, including the mean slope (Rebuttal Figure 1A, SFig 1F), the standard deviation in slopes (Rebuttal Figure 1B, SFig 1G) as well as the Precision vs. Accuracy tradeoff (Rebuttal Figure 1C, SFig 1H). We therefore think that our results are well in line with prior literature, even though a direct comparison remains difficult due to differences in the task.

In response to the reviewer’s comment, and related to their first comment, we made the following addition to the discussion section.

Page 12: This suggests that different regions encode distinct task regularities in parallel to form optimal sensorimotor representations to balance specificity and regularization. This is well in line with our behavioral results, showing that TTC-task performance became more optimal in the face of both of these two objectives. Over time, behavioral responses clustered more closely between the diagonal and the average line in the behavioral response profile (Fig. 1B, S1G), and the TTC error decreased over time. While different participants approached these optimal performance levels from different directions, either starting with good performance or strong regularization, the group approached overall optimal performance levels over the course of the experiment.

3) I am curious to know whether differences between high-accuracy andmedium-accuracy feedback as well as between medium-accuracy and low-accuracy feedback predicted hippocampal activity in the first GLM analysis (middle page 5). Currently, the authors only present the findings for the contrast between high-accuracy and low-accuracy feedback. Examining all feedback levels may provide additional insight into the nature of hippocampal involvement and is perhaps more consistent with the subsequent GLM analysis (bottom page 6) in which, according to my understanding, all improvements across subsequent trials were considered (i.e., from low-accuracy to medium-accuracy; medium-accuracy to high-accuracy; as well as low-accuracy to high-accuracy).

We thank the reviewer for this thoughtful question, which relates to questions 5 by reviewer 1. The reviewer is correct that the contrast shown in Fig 2 does not consider the medium-accuracy feedback levels, and that the model in itself is slightly different from the one used in the subsequent analysis presented in Fig. 3. To reply to this comment as well as to a related one by reviewer 1 together, we therefore repeated the full analysis while modeling the three feedback levels in one parametric regressor, which includes the medium-accuracy feedback trials, and is consistent with the analysis shown in Fig. 3. The results of this new analysis are presented in the new Supplementary Fig. 3B.

In short, the model included one parametric regressor with three levels reflecting the three types of feedback, and all nuisance regressors remained unchanged. Instead of contrasting high vs. low accuracy feedback, we then performed voxel-wise t-tests on the beta estimates obtained for the parametric feedback regressor. We found that our results presented initially were very robust: Both the observed clusters in the voxel-wise analysis (on whole-brain FWE-corrected levels) as well as the ROI results replicated across the two analyses, and our conclusions therefore remain unchanged.

We made multiple textual additions to the manuscript to include this new analysis, and we present the results of the analysis including a direct comparison to our initial results in the new Supplementary Fig. 3. Following textual additions were.

Page 5: Note that these results were robust even when fewer nuisance regressors were included to control for model over-specification (Fig. S3B; two-tailed one-sample t tests: anterior HPC, t(33) = -3.65, p = 8.9x10-4, pfwe = 0.002, d=-0.63, CI: [-1.01, -0.26]; posterior HPC, t(33) = -1.43, p = 0.161, pfwe = 0.322, d=-0.25, CI: [-0.59, 0.10]), and when all three feedback levels were modeled with one parametric regressors (Fig. S3C; two-tailed one-sample t tests: anterior HPC, t(33) = -3.59, p = 0.002, pfwe = 0.005, d=-0.56, CI: [-0.93, -0.20]; posterior HPC, t(33) = -0.99, p = 0.329, pfwe = 0.659, d=-0.17, CI: [-0.51, 0.17]). Further, there was no systematic relationship between subsequent trials on a behavioral level [...]

Page 17: Moreover, instead of modeling the three feedback levels with three independent regressors, we repeated the analysis modeling the three feedback levels as one parametric regressor with three levels. All other regressors remained unchanged, and the model included the regressors for ITIs and ISIs. We then conducted t-tests implemented in SPM12 using thebeta estimates obtained for the parametric feedback regressor (Fig. S2C). Compared to the initial analyses presented above, this has the advantage that medium-accuracy feedback trials are considered for the statistics as well.

4) The authors modeled the inter-trial intervals and periods of rest in their univariateGLMs. This approach of modelling all 'down time' can lead to model over-specification and inaccurate parameter estimation (e.g. Pernet, 2014). A comment on this approach as well as consideration of not modelling the inter-trial intervals would be useful.

This is an important issue that we did not address in our initial manuscript. We are aware and agree with the reviewer’s general concern about model over-specification, which can be a big problem in regression as it leads to biased estimates. We did examine whether our model was overspecified before running it, but we did not report a formal test of it in the manuscript. We are grateful to be given the opportunity to do so now.

In response to the reviewer’s comment, we repeated the full analysis shown in Fig. 2 while excluding the nuisance regressors for inter-trial intervals (ISI) and breaks (or inter-session intervals, ISI). All other regressors and analysis steps stayed unchanged relative to the one reported in Fig. 2. The new results are presented in a new Supplementary Figure 3B.

Like for our previous analysis, we again see that the results we initially presented were extremely robust even on whole-brain FWE corrected levels, as well as on ROI level. Our conclusions therefore remain unchanged, and the results we presented initially are not affected by potential model overspecification. In addition to the new Supplementary Figure 3B, we made multiple textual changes to the manuscript to describe this new analysis and its implications. Note that we used the same nuisance regressors in all other GLM analyses too, meaning that it is also very unlikely that model overspecification affects any of the other results presented. We thank the reviewer for suggesting this analysis, and we feel including it in the manuscript has further strengthened the points we initially made.

Following additions were made to the manuscript.

Page 16: The GLM included three boxcar regressors modeling the feedback levels, one for ITIs, one for button presses and one for periods of rest (inter-session interval, ISI) [...]

Page 16: ITIs and ISIs were modeled to reduce task-unrelated noise, but to ensure that this did not lead to over-specification of the above-described GLM, we repeated the full analysis without modeling the two. All other regressors including the main feedback regressors of interest remained unchanged, and we repeated both the voxel-wise and ROI-wise statistical tests as described above (Fig. S2B).

Page 17: Note that these results were robust even when fewer nuisance regressors were included to control for model over-specification (Fig. S3B; two-tailed one-sample t tests: anterior HPC, t(33) = -3.65, p = 8.9x10-4, pfwe = 0.002, d=-0.63, CI: [-1.01, -0.26]; posterior HPC, t(33) = -1.43, p = 0.161, pfwe = 0.322, d=-0.25, CI: [-0.59, 0.10]), and when all three feedback levels were modeled with one parametric regressors (Fig. S3C; two-tailed one-sample t tests: anterior HPC, t(33) = -3.59, p = 0.002, pfwe = 0.005, d=-0.56, CI: [-0.93, -0.20]; posterior HPC, t(33) = -0.99, p = 0.329, pfwe = 0.659, d=-0.17, CI: [-0.51, 0.17]). Further, there was no systematic relationship between subsequent trials on a behavioral level [...]

Reviewer #3 (Public Review):

This paper reports the results of an interesting fMRI study examining the neural correlates of time estimation with an elegant design and a sensorimotor timing task. Results show that hippocampal activity and connectivity are modulated by performance on the task as well as the valence of the feedback provided. This study addresses a very important question in the field which relates to the function of the hippocampus in sensorimotor timing. However, a lack of clarity in the description of the MRI results (and associated methods) currently prevents the evaluation of the results and the interpretations made by the authors. Specifically, the model testing for timing-specific/timing-independent effects is questionable and needs to be clarified. In the current form, several conclusions appear to not be fully supported by the data.

We thank the reviewer for pointing us to many methodological points that needed clarification. We apologize for the confusion about our methods, which we clarify in the revised manuscript. Please find our responses to the individual points below.

Major points

Some methodological points lack clarity which makes it difficult to evaluate the results and the interpretation of the data.

We really appreciate the many constructive comments below. We feel that clarifying these points improved our manuscript immensely.

1) It is unclear how the 3 levels of accuracy and feedback (high, medium, and lowperformance) were computed. Please provide the performance range used for this classification. Was this adjusted to the participants' performance?

The formula that describes how the response window was computed for the different speed levels was reported in the methods section of the original manuscript on page 13. It reads as follows:

“The following formula was used to scale the response window width: d ± ((k ∗ d)/2) where d is the target TTC and k is a constant proportional to 0.3 and 0.6 for high and medium accuracy, respectively.“

In response to the reviewer’s comment, we now additionally report the exact ranges of the different response windows in a new Supplementary Table 1 and refer to it in the Methods section as follows.

Page 10: To calibrate performance feedback across different TTC durations, the precise response window widths of each feedback level scaled with the speed of the fixation target (Table S1).

2) The description of the MRI results lacks details. It is not always clear in the resultssection which models were used and whether parametric modulators were included or not in the model. This makes the results section difficult to follow. For example,

a) Figure 2: According to the description in the text, it appears that panels A and B report the results of a model with 3 regressors, ie one for each accuracy/feedback level (high, medium, low) without parametric modulators included. However, the figure legend for panel B mentions a parametric modulator suggesting that feedback was modelled for each trial as a parametric modulator. The distinction between these 2 models must be clarified in the result section.

We thank the reviewer very much for spotting this discrepancy. Indeed, Figure 2 shows the results obtained for a GLM in which we modeled the three feedback levels with separate regressors, not with one parametric regressor. Instead, the latter was the case for Figure 3. We apologize for the confusion and corrected the description in the figure caption, which now reads as follows. The description in the main text and the methods remain unchanged.

Caption Fig. 2: We plot the beta estimates obtained for the contrast between high vs. low feedback.

Moreover, note that in response to comment 5 by reviewer 1 and comment 3 by reviewer 2, the revised manuscript now additionally reports the results obtained for the parametric regressor in the new Supplementary Figure 3C. All conclusions remain unchanged.

Additionally, it is unclear how Figure 2A supports the following statement: "Moreover, the voxel-wise analysis revealed similar feedback-related activity in the thalamus and the striatum (Fig. 2A), and in the hippocampus when the feedback of the current trial was modeled (Fig. S3)." This is confusing as Figure 2A reports an opposite pattern of results between the striatum/thalamus and the hippocampus. It appears that the statement highlighted above is supported by results from a model including current trial feedback as a parametric modulator (reported in Figure S3).

We agree with the reviewer that our result description was confusing and changed it. It now reads as follows.

Page 5: Moreover, the voxel-wise analysis revealed feedback-related activity also in the thalamus and the striatum (Fig. 2A) [...]

Also, note that it is unclear from Figure 2A what is the direction of the contrast highlighting the hippocampal cluster (high vs. low according to the text but the figure shows negative values in the hippocampus and positive values in the thalamus). These discrepancies need to be addressed and the models used to support the statements made in the results sections need to be explicitly described.

The description of the contrast is correct. Negative values indicate smaller errors and therefore better feedback, which is mentioned in the caption of Fig. 2 as follows:

“Negative values indicate that smaller errors, and higher-accuracy feedback, led to stronger activity.”

Note that the timing error determined the feedback, and that we predicted stronger updating and therefore stronger activity for larger errors (similar to a prediction error). We found the opposite. We mention the reasoning behind this analysis at various locations in the manuscript e.g. when talking about the connectivity analysis:

“We reasoned that larger timing errors and therefore low-accuracy feedback would result in stronger updating compared to smaller timing errors and high-accuracy feedback”

In response to the reviewer’s remark, we clarified this further by adding the following statement to the result section.

Page 5: “Using a mass-univariate general linear model (GLM), we modeled the three feedback levels with one regressor each plus additional nuisance regressors (see methods for details). The three feedback levels (high, medium and low accuracy) corresponded to small, medium and large timing errors, respectively. We then contrasted the beta weights estimated for high-accuracy vs. low-accuracy feedback and examined the effects on group-level averaged across runs.”

b) Connectivity analyses: It is also unclear here which model was used in the PPIanalyses presented in Figure 2. As it appears that the seed region was extracted from a high vs. low contrast (without modulators), the PPI should be built using the same model. I assume this was the case as the authors mentioned "These co-fluctuations were stronger when participants performed poorly in the previous trial and therefore when they received low-accuracy feedback." if this refers to low vs. high contrast. Please clarify.

Yes, the PPI model was built using the same model. We clarified this in the methods section by adding the following statement to the PPI description.

Page 17: “The PPI model was built using the same model that revealed the main effects used to define the HPC sphere “

Yes, the reviewer is correct in thinking that the contrast shows the difference between low vs. high-accuracy feedback. We clarified this in the main text as well as in the caption of Fig. 2.

Caption Fig 2: [...] We plot results of a psychophysiological interactions (PPI) analysis conducted using the hippocampal peak effects in (A) as a seed for low vs. high-accuracy feedback. [...]

Page 17: The estimated beta weight corresponding to the interaction term was then tested against zero on the group-level using a t-test implemented in SPM12 (Fig. 2C). The contrast reflects the difference between low vs. high-accuracy feedback. This revealed brain areas whose activity was co-varying with the hippocampus seed ROI as a function of past-trial performance (n-1).

c) It is unclear why the model testing TTC-specific / TTC-independent effects (resultspresented in Figure 3) used 2 parametric modulators (as opposed to building two separate models with a different modulator each). I wonder how the authors dealt with the orthogonalization between parametric modulators with such a model. In SPM, the orthogonalization of parametric modulators is based on the order of the modulators in the design matrix. In this case, parametric modulator #2 would be orthogonalized to the preceding modulator so that a contrast focusing on the parametric modulator #2 would highlight any modulation that is above and beyond that explained by modulator #1. In this case, modulation of brain activity that is TTC-specific would have to be above and beyond a modulation that is TTC-independent to be highlighted. I am unsure that this is what the authors wanted to test here (or whether this is how the MRI design was built). Importantly, this might bias the interpretation of their results as - by design - it is less likely to observe TTC-specific modulations in the hippocampus as there is significant TTC-independent modulation. In other words, switching the order of the modulators in the model (or building two separate models) might yield different results. This is an important point to address as this might challenge the TTC-specific/TTC-independent results described in the manuscript.

We thank the reviewer for raising this important issue. When running the respective analysis, we made sure that the regressors were not collinear and we therefore did not expect substantial overlap in shared variance between them. However, we agree with the reviewer that orthogonalizing one regressor with respect to the other could still affect the results. To make sure that our expectations were indeed met, we therefore repeated the main analysis twice: 1) switching the order of the modulators and 2) turning orthogonalization off (which is possible in SPM12 unlike in previous versions). In all cases, our key results and conclusions remained unchanged, including the central results of the hippocampus analyses.

Anterior (ant.) / Posterior (post.) Hippocampus ROI analysis with A) original order of modulators, B) switching the order of the modulators and C) turning orthogonalization of modulators off. ABC) Orange color corresponds to the TTC-independent condition whereas light-blue color corresponds to the TTC-specific condition. Statistics reflect p<0.05 at Bonferroni corrected levels () obtained using a group-level one-tailed one-sample t-test against zero; A) pfwe = 0.017, B) pfwe = 0.039, C) pfwe = 0.039.*

Because orthogonalization did not affect the conclusions, the new manuscript simply reports the analysis for which it was turned off. Note that these new figures are extremely similar to the original figures we presented, which can be seen in the exemplary figure below showing our key results at a liberal threshold for transparency. In addition, we clarified that orthogonalization was turned off in the methods section as follows.

Page 18: These two regressors reflect the tests for target-TTC-independent and target-TTC-specific updating, respectively, and they were not orthogonalized to each other.

Comparison of old & new results: also see Fig. 3 and Fig. S5 in manuscript

d) It is also unclear how the behavioral improvement was coded/classified "wecontrasted trials in which participants had improved versus the ones in which they had not improved or got worse"- It appears that improvement computation was based on the change of feedback valence (between high, medium and low). It is unclear why performance wasn't used instead? This would provide a finer-grained modulation?

We thank the reviewer for the opportunity to clarify this important point. First, we chose to model feedback because it is the feedback that determines whether participants update their “internal model” or not. Without feedback, they would not know how well they performed, and we would not expect to find activity related to sensorimotor updating. Second, behavioral performance and received feedback are tightly correlated, because the former determines the latter. We therefore do not expect to see major differences in results obtained between the two. Third, we did in fact model both feedback and performance in two independent GLMs, even though the way the results were reported in the initial submission made it difficult to compare the two.

Figure 4 shows the results obtained when modeling behavioral performance in the current trial as an F-contrast, and Supplementary Fig 4 shows the results when modeling the feedback received in the current trial as a t-contrast. While the voxel-wise t-maps/F-maps are also quite similar, we now additionally report the t-contrast for the behavioral-performance GLM in a new Supplementary Figure 4C. The t-maps obtained for these two different analyses are extremely similar, confirming that the direction of the effects as well as their interpretation remain independent of whether feedback or performance is modeled.

The revised manuscript refers to the new Supplementary Figure 4C as follows.

Page 17: In two independent GLMs, we analyzed the time courses of all voxels in the brain as a function of behavioral performance (i.e. TTC error) in each trial, and as a function of feedback received at the end of each trial. The models included one mean-centered parametric regressor per run, modeling either the TTC error or the three feedback levels in each trial, respectively. Note that the feedback itself was a function of TTC error in each trial [...] We estimated weights for all regressors and conducted a t-test against zero using SPM12 for our feedback and performance regressors of interest on the group level (Fig. S4A). [...]

Page 17: In addition to the voxel-wise whole-brain analyses described above, we conducted independent ROI analyses for the anterior and posterior sections of the hippocampus (Fig. S2A). Here, we tested the beta estimates obtained in our first-level analysis for the feedback and performance regressors of interest (Fig. S4B; two-tailed one-sample t tests: anterior HPC, t(33) = -5.92, p = 1.2x10-6, pfwe = 2.4x10-6, d=-1.02, CI: [-1.45, -0.6]; posterior HPC, t(33) = -4.07, p = 2.7x10-4, pfwe = 5.4x10-4, d=-0.7, CI: [-1.09, -0.32]). See section "Regions of interest definition and analysis" for more details.

If the feedback valence was used to classify trials as improved or not, how was this modelled (one regressor for improved, one for no improvement? As opposed to a parametric modulator with performance improvement?).

We apologize for the lack of clarity regarding our regressor design. In response to this comment, we adapted the corresponding paragraph in the methods to express more clearly that improvement trials and no-improvement trials were modeled with two separate parametric regressors - in line with the reviewer’s understanding. The new paragraph reads as follows.

Page 18: One regressor modeled the main effect of the trial and two parametric regressors modeled the following contrasts: Parametric regressor 1: trials in which behavioral performance improved \textit{vs}. parametric regressor 2: trials in which behavioral performance did not improve or got worse relative to the previous trial.

Last, it is also unclear how ITI was modelled as a regressor. Did the authors mean a parametric modulator here? Some clarification on the events modelled would also be helpful. What was the onset of a trial in the MRI design? The start of the trial? Then end? The onset of the prediction time?

The Inter-trial intervals (ITIs) were modeled as a boxcar regressor convolved with the hemodynamic response function. They describe the time after the feedback-phase offset and the subsequent trial onset. Moreover, the start of the trial was the moment when the visual-tracking target started moving after the ITI, whereas the trial end was the offset of the feedback phase (i.e. the moment in which the feedback disappeared from the screen). The onset of the “prediction time” was the moment in which the visual-tracking target stopped moving, prompting participants to estimate the time-to-contact. We now explain this more clearly in the methods as shown below.

Page 16: The GLM included three boxcar regressors modeling the feedback levels, one for ITIs, one for button presses and one for periods of rest (inter-session interval, ISI), which were all convolved with the canonical hemodynamic response function of SPM12. The start of the trial was considered as the trial onsets for modeling (i.e. the time when the visual-tracking target started moving). The trial end was the offset of the feedback phase (i.e. the moment in which the feedback disappeared from the screen). The ITI was the time between the offset of the feedback-phase and the subsequent trial onset.

On a related note, in response to question 4 by reviewer 2, we now repeated one of the main analyses (Fig. 2) without modeling the ITI (as well as the Inter-session interval, ISI). We found that our key results and conclusions are independent of whether or not these time points were modeled. These new results are presented in the new Supplementary Figure 3B.

Page 16: ITIs and ISIs were modeled to reduce task-unrelated noise, but to ensure that this did not lead to over-specification of the above-described GLM, we repeated the full analysis without modeling the two. [...]

1. Perhaps as a result of a lack of clarity in the result section and the MRI methods, it appears that some conclusions presented in the result section are not supported by the data. E.g. "Instead, these results are consistent with the notion that hippocampal activity signals the updating of task-relevant sensorimotor representations in real-time." The data show that hippocampal activity is higher during and after an accurate trial. This pattern of results could be attributed to various processes such as e.g. reward or learning etc. I would recommend not providing such interpretations in the result section and addressing these points in the discussion.

Similar to above, statements like "These results suggest that the hippocampus updates information that is independent of the target TTC". The data show that higher hippocampal activity is linked to greater improvement across trials independent of the timing of the trial. The point about updating is rather speculative and should be presented in the discussion instead of the result section.

The reviewer is referring to two statements in the results section that reflect our interpretation rather than a description of the results. In response to the reviewer’s comment, we therefore removed the following statement from the results.

Instead, these results are consistent with the notion that hippocampal activity signals the updating of task-relevant sensorimotor representations in real-time.

In addition, we replaced the remaining statement by the following. We feel this new statement makes clear why we conducted the analysis that is described without offering an interpretation of the results that were presented before.

Page 8: We reasoned that updating TTC-independent information may support generalization performance by means of regularizing the encoded intervals based on the temporal context in which they were encoded.

Author Response:

Reviewer #1 (Public Review):

The manuscript provides very high quality single-cell physiology combined with population physiology to reveal distinctives roles for two anatomically dfferent LN populations in the cockroach antennal lobe. The conclusion that non-spiking LNs with graded responses show glomerular-restricted responses to odorants and spiking LNs show similar responses across glomeruli generally supported with strong and clean data, although the possibility of selective interglomerular inhibition has not been ruled out. On balance, the single-cell biophysics and physiology provides foundational information useful for well-grounded mechanistic understanding of how information is processed in insect antennal lobes, and how each LN class contributes to odor perception and behavior.

Thank you for this positive feedback.

Reviewer #2 (Public Review):

The manuscript "Task-specific roles of local interneurons for inter- and intraglomerular signaling in the insect antennal lobe" evaluates the spatial distribution of calcium signals evoked by odors in two major classes of olfactory local neurons (LNs) in the cockroach P. Americana, which are defined by their physiological and morphological properties. Spiking type I LNs have a patchy innervation pattern of a subset of glomeruli, whereas non-spiking type II LNs innervate almost all glomeruli (Type II). The authors' overall conclusion is that odors evoke calcium signals globally and relatively uniformly across glomeruli in type I spiking LNs, and LN neurites in each glomerulus are broadly tuned to odor. In contrast, the authors conclude that they observe odor-specific patterns of calcium signals in type II nonspiking LNs, and LN neurites in different glomeruli display distinct local odor tuning. Blockade of action potentials in type I LNs eliminates global calcium signaling and decorrelates glomerular tuning curves, converting their response profile to be more similar to that of type II LNs. From these conclusions, the authors infer a primary role of type I LNs in interglomerular signaling and type III LNs in intraglomerular signaling.

The question investigated by this study - to understand the computational significance of different types of LNs in olfactory circuits - is an important and significant problem. The design of the study is straightforward, but methodological and conceptual gaps raise some concerns about the authors' interpretation of their results. These can be broadly grouped into three main areas.

1) The comparison of the spatial (glomerular) pattern of odor-evoked calcium signals in type I versus type II LNs may not necessarily be a true apples-to-apples comparison. Odor-evoked calcium signals are an order of magnitude larger in type I versus type II cells, which will lead to a higher apparent correlation in type I cells. In type IIb cells, and type I cells with sodium channel blockade, odor-evoked calcium signals are much smaller, and the method of quantification of odor tuning (normalized area under the curve) is noisy. Compare, for instance, ROI 4 & 15 (Figure 4) or ROI 16 & 23 (Figure 5) which are pairs of ROIs that their quantification concludes have dramatically different odor tuning, but which visual inspection shows to be less convincing. The fact that glomerular tuning looks more correlated in type IIa cells, which have larger, more reliable responses compared to type IIb cells, also supports this concern.

We agree with the reviewer that "the comparison of the spatial (glomerular) pattern of odor-evoked calcium signals is not necessarily a true apples-to-apples comparison". Type I and type II LNs are different neuron types. Given their different physiology and morphology, this is not even close to a "true apples-to-apples comparison" - and a key point of the manuscript is to show just that.

As we have emphasized in response to Essential Revision 1, the differences in Ca2+ signals are not an experimental shortcoming but a physiologically relevant finding per se. These data, especially when combined with the electrophysiological data, contribute to a better understanding of these neurons’ physiological and computational properties.

It is physiologically determined that the Ca2+ signals during odorant stimulation in the type II LNs are smaller than in type I LNs. And yes, the signals are small because small postsynpathetic Ca2+ currents predominantly cause the signals. Regardless of the imaging method, this naturally reduces the signal-to-noise ratio, making it more challenging to detect signals. To address this issue, we used a well-defined and reproducible method for analyzing these signals. In this context, we do not agree with the very general criticism of the method. The reviewer questions whether the signals are odorant-induced or just noise (see also minor point 12). If we had recorded only noise, we would expect all tuning curves (for each odorant and glomerulus) to be the same. In this context, we disagree with the reviewer's statement that the tuning curves do not represent the Ca2+ signals in Figure 4 (ROI 4 and 15) and Figure 5 (ROI 16 and 23). This debate reflects precisely the kind of 'visual inspection bias' that our clearly defined analysis aims to avoid. On close inspection, the differences in Ca2+ signals can indeed be seen. Figure II (of this letter) shows the signals from the glomeruli in question at higher magnification. The sections of the recordings that were used for the tuning curves are marked in red.

Figure II: Ca2+ signals of selected glomeruli that were questioned by the reviewer.

2) An additional methodological issue that compounds the first concern is that calcium signals are imaged with wide-field imaging, and signals from each ROI likely reflect out of plane signals. Out of plane artifacts will be larger for larger calcium signals, which may also make it impossible to resolve any glomerular-specific signals in the type I LNs.

Thank you for allowing us to clarify this point. The reviewer comment implies that the different amplitudes of the Ca2+ signals indicate some technical-methodological deficiency (poorly chosen odor concentration). But in fact, this is a key finding of this study that is physiologically relevant and crucial for understanding the function of the neurons studied. These very differences in the Ca2+ signals are evidence of the different roles these neurons play in AL. The different signal amplitudes directly show the distinct physiology and Ca2+ sources that dominate the Ca2+ signals in type I and type II LNs. Accordingly, it is impractical to equalize the magnitude of Ca2+ signals under physiological conditions by adjusting the concentration of odor stimuli.

In the following, we address these issues in more detail: 1) Imaging Method 2) Odorant stimulation 3) Cell type-specific Ca2+ signals

1) Imaging Method:

Of course, we agree with the reviewer comment that out-of-focus and out-of-glomerulus fluorescence can potentially affect measurements, especially in widefield optical imaging in thick tissue. This issue was carefully addressed in initial experiments. In type I LNs, which innervate a subset of glomeruli, we detected fluorescence signals, which matched the spike pattern of the electrophysiological recordings 1:1, only in the innervated glomeruli. In the not innervated ROIs (glomeruli), we detected no or comparatively very little fluorescence, even in glomeruli directly adjacent to innervated glomeruli.

To illustrate this, FIGURE I (of this response letter) shows measurements from an AL in which an uniglomerular projection neuron was investigated in an a set of experiments that were not directly related to the current study. In this experiment, a train of action potential was induced by depolarizing current. The traces show the action potential induced fluorescent signals from the innervated glomerulus (glomerulus #1) and the directly adjacent glomeruli.

These results do not entirely exclude that the large Ca2+ signals from the innervated LN glomeruli may include out-of-focus and out-of-glomerulus fluorescence, but they do show that the bulk of the signal is generated from the recorded neuron in the respective glomeruli.

Figure I: Simultaneous electrophysiological and optophysiological recordings of a uniglomerular projection using the ratiometric Ca2+ indicator fura-2. The projection neuron has its arborization in glomerulus 1. The train of action potentials was induced with a depolarizing current pulse (grey bar).

2) Odorant Stimulation: It is important to note that the odorant concentration cannot be varied freely. For these experiments, the odorant concentrations have to be within a 'physiologically meaningful' range, which means: On the one hand, they have to be high enough to induce a clear response in the projection neurons (the antennal lobe output). On the other hand, however, the concentration was not allowed to be so high that the ORNs were stimulated nonspecifically. These criteria were met with the used concentrations since they induced clear and odorant-specific activity in projection neurons.

3) Cell type-specific Ca2+ signals:

The differences in Ca2+ signals are described and discussed in some detail throughout the text (e.g., page 6, lines 119-136; page 9, lines 193-198; page 10-11, lines 226-235; page 14-15, line 309-333). Briefly: In spiking type I LNs, the observed large Ca2+ signals are mediated mainly by voltage-depended Ca2+ channels activated by the Na+-driven action potential's strong depolarization. These large Ca2+ signals mask smaller signals that originate, for example, from excitatory synaptic input (i.e., evoked by ligand-activated Ca2+ conductances). Preventing the firing of action potentials can unmask the ligand-activated signals, as shown in Figure 4 (see also minor comments 8. and 10.). In nonspiking type II LNs, the action potential-generated Ca2+ signals are absent; accordingly, the Ca2+ signals are much smaller. In our model, the comparatively small Ca2+ signals in type II LNs are mediated mainly by (synaptic) ligand-gated Ca2+ conductances, possibly with contributions from voltage-gated Ca2+ channels activated by the comparatively small depolarization (compared with type I LNs).

Accordingly, our main conclusion, that spiking LNs play a primary role in interglomerular signaling, while nonspiking LNs play an essential role in intraglomeular signaling, can be DIRECTLY inferred from the differences in odorant induced Ca2+ signals alone.

a) Type I LN: The large, simultaneous, and uniform Ca2+ signals in the innervated glomeruli of an individual type I LN clearly show that they are triggered in each glomerulus by the propagated action potentials, which conclusively shows lateral interglomerular signal propagation.

b) Type II LNs: In the type II LNs, we observed relatively small Ca2+ signals in single glomeruli or a small fraction of glomeruli of a given neuron. Importantly, the time course and amplitude of the Ca2+ signals varied between different glomeruli and different odors. Considering that type II LNs in principle, can generate large voltage-activated Ca2+ currents (larger that type I LNS; page 4, lines 82-86, Husch et al. 2009a,b; Fusca and Kloppenburg 2021), these data suggest that in type II LNs electrical or Ca2+ signals spread only within the same glomerulus; and laterally only to glomeruli that are electrotonically close to the odorant stimulated glomerulus.

Taken together, this means that our conclusions regarding inter- and intraglomerular signaling can be derived from the simultaneously recorded amplitudes and the dynamics of the membrane potential and Ca2+ signals alone. This also means that although the correlation analyses support this conclusion nicely, the actual conclusion does not ultimately depend on the correlation analysis. We had (tried to) expressed this with the wording, “Quantitatively, this is reflected in the glomerulus-specific odorant responses and the diverse correlation coefficiiants across…” (page 10, lines 216-217) and “ …This is also reflected in the highly correlated tuning curves in type I LNs and low correlations between tuning curves in type II LNs”(page 13, lines 293-295).

3) Apart from the above methodological concerns, the authors' interpretation of these data as supporting inter- versus intra-glomerular signaling are not well supported. The odors used in the study are general odors that presumably excite feedforward input to many glomeruli. Since the glomerular source of excitation is not determined, it's not possible to assign the signals in type II LNs as arising locally - selective interglomerular signal propagation is entirely possible. Likewise, the study design does not allow the authors to rule out the possibility that significant intraglomerular inhibition may be mediated by type I LNs.

The reviewer addresses an important point. However, from the comment, we get the impression that he/she has not taken into account the entire data set and the DISCUSSION. In fact, this topic has already been discussed in some detail in the original version (page 12, lines 268-271; page 15-16; lines 358-374). This section even has a respective heading: "Inter- and intraglomerular signaling via nonspiking type II LNs" (page 15, line 338). We apologize if our explanations regarding this point were unclear, but we also feel that the reviewer is arguing against statements that we did not make in this way.

a) In 11 out of 18 type II LNs we found 'relatively uncorrelated' (r=0.43±0.16, N=11) glomerular tuning curves. These experiments argue strongly for a 'local excitation' with restricted signal propagation and do not provide support for interglomerular signal propagation. Thus, these results support our interpretation of intraglomerular signaling in this set of neurons.

b) In 7 out of 18 experiments, we observed 'higher correlated' glomerular tuning curves (r=0.78±0.07, N=7). We agree with the reviewer that this could be caused by various mechanisms, including simultaneous input to several glomeruli or by interglomerular signaling. Both possibilities were mentioned and discussed in the original version of the manuscript (page 12, lines 268-271; page 15-16; lines 358-374). In the Discussion, we considered the latter possibility in particular (but not exclusively) for the type IIa1 neurons that generate spikelets. Their comparatively stronger active membrane properties may be particularly suitable for selective signal transduction between glomeruli.

c) We have not ruled out that local signaling exists in type I LNs – in addition to interglomerular signaling. The highly localized Ca2+ signals in type I LNs, which we observed when Na+ -driven action potential generation was prevented, may support this interpretation. However, we would like to reiterate that the simultaneous electrophysiological and optophysiological recordings, which show highly correlated glomerular Ca2+ dynamics that match 1:1 with the simultaneously recorded action potential pattern, clearly suggest interglomerular signaling. We also want to emphasize that this interpretation is in agreement with previous models derived from electrophysiological studies(Assisi et al., 2011; Fujiwara et al., 2014; Hong and Wilson, 2015; Nagel and Wilson, 2016; Olsen and Wilson, 2008; Sachse and Galizia, 2002; Wilson, 2013).

In light of the reviewer's comment(s), we have modified the text to clarify these points (page 14, lines 317-319).

Reviewer #3 (Public Review):

To elucidate the role of the two types of LNs, the authors combined whole-cell patch clamp recordings with calcium imaging via single cell dye injection. This method enables to monitor calcium dynamics of the different axons and branches of single LNs in identified glomeruli of the antennal lobe, while the membrane potential can be recorded at the same time. The authors recorded in total from 23 spiking (type I LN) and 18 non-spiking (type II LN) neurons to a set of 9 odors and analyzed the firing pattern as well as calcium signals during odor stimulation for individual glomeruli. The recordings reveal on one side that odor-evoked calcium responses of type I LNs are odor-specific, but homogeneous across glomeruli and therefore highly correlated regarding the tuning curves. In contrast, odor-evoked responses of type II LNs show less correlated tuning patterns and rather specific odor-evoked calcium signals for each glomerulus. Moreover the authors demonstrate that both LN types exhibit distinct glomerular branching patterns, with type I innervating many, but not all glomeruli, while type II LNs branch in all glomeruli.

From these results and further experiments using pharmacological manipulation, the authors conclude that type I LNs rather play a role regarding interglomerular inhibition in form of lateral inhibition between different glomeruli, while type II LNs are involved in intraglomerular signaling by developing microcircuits in individual glomeruli.

In my opinion the methodological approach is quite challenging and all subsequent analyses have been carried out thoroughly. The obtained data are highly relevant, but provide rather an indirect proof regarding the distinct roles of the two LN types investigated. Nevertheless, the conclusions are convincing and the study generally represents a valuable and important contribution to our understanding of the neuronal mechanisms underlying odor processing in the insect antennal lobe. I think the authors should emphasize their take-home messages and resulting conclusions even stronger. They do a good job in explaining their results in their discussion, but need to improve and highlight the outcome and meaning of their individual experiments in their results section.

Thank you for this positive feedback.

References:

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Das, S., Trona, F., Khallaf, M.A., Schuh, E., Knaden, M., Hansson, B.S., Sachse, S., 2017. Electrical synapses mediate synergism between pheromone and food odors in Drosophila melanogaster . Proc Natl Acad Sci U S A 114, E9962–E9971. https://doi.org/10.1073/pnas.1712706114

Fujiwara, T., Kazawa, T., Haupt, S.S., Kanzaki, R., 2014. Postsynaptic odorant concentration dependent inhibition controls temporal properties of spike responses of projection neurons in the moth antennal lobe. PLOS ONE 9, e89132. https://doi.org/10.1371/journal.pone.0089132

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Husch, A., Paehler, M., Fusca, D., Paeger, L., Kloppenburg, P., 2009b. Distinct electrophysiological properties in subtypes of nonspiking olfactory local interneurons correlate with their cell type-specific Ca2+ current profiles. J Neurophysiol 102, 2834–2845. https://doi.org/10.1152/jn.00627.2009

Nagel, K.I., Wilson, R.I., 2016. Mechanisms Underlying Population Response Dynamics in Inhibitory Interneurons of the Drosophila Antennal Lobe. J Neurosci 36, 4325–4338. https://doi.org/10.1523/JNEUROSCI.3887-15.2016

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Author Response

Reviewer #1 (Public Review):

In computational modeling studies of behavioral data using reinforcement learning models, it has been implicitly assumed that parameter estimates generalize across tasks (generalizability) and that each parameter reflects a single cognitive function (interpretability). In this study, the authors examined the validity of these assumptions through a detailed analysis of experimental data across multiple tasks and age groups. The results showed that some parameters generalize across tasks, while others do not, and that interpretability is not sufficient for some parameters, suggesting that the interpretation of parameters needs to take into account the context of the task. Some researchers may have doubted the validity of these assumptions, but to my knowledge, no study has explicitly examined their validity. Therefore, I believe this research will make an important contribution to researchers who use computational modeling. In order to clarify the significance of this research, I would like the authors to consider the following points.

1) Effects of model misspecification

In general, model parameter estimates are influenced by model misspecification. Specifically, if components of the true process are not included in the model, the estimates of other parameters may be biased. The authors mentioned a little about model misspecification in the Discussion section, but they do not mention the possibility that the results of this study itself may be affected by it. I think this point should be discussed carefully.

The authors stated that they used state-of-the-art RL models, but this does not necessarily mean that the models are correctly specified. For example, it is known that if there is history dependence in the choice itself and it is not modeled properly, the learning rates depending on valence of outcomes (alpha+, alpha-) are subject to biases (Katahira, 2018, J Math Pscyhol). In the authors' study, the effect of one previous choice was included in the model as choice persistence, p. However, it has been pointed out that not including the effect of a choice made more than two trials ago in the model can also cause bias (Katahira, 2018). The authors showed taht the learning rate for positive RPE, alpha+ was inconsistent across tasks. But since choice persistence was included only in Task B, it is possible that the bias of alpha+ was different between tasks due to individual differences in choice persistence, and thus did not generalize.

However, I do not believe that it is necessary to perform a new analysis using the model described above. As for extending the model, I don't think it is possible to include all combinations of possible components. As is often said, every model is wrong, and only to varying degrees. What I would like to encourage the authors to do is to discuss such issues and then consider their position on the use of the present model. Even if the estimation results of this model are affected by misspecification, it is a fact that such a model is used in practice, and I think it is worthwhile to discuss the nature of the parameter estimates.

We thank the reviewer for this thoughtful question, and have added the following paragraph to the discussion section that is aims to address it:

“Another concern relates to potential model misspecification and its effects on model parameter estimates: If components of the true data-generating process are not included in a model (i.e., a model is misspecified), estimates of existing model parameters may be biased. For example, if choices have an outcome-independent history dependence that is not modeled properly, learning rate parameters have shown to be biased [63]. Indeed, we found that learning rate parameters were inconsistent across the tasks in our study, and two of our models (A and C) did not model history dependence in choice, while the third (model B) only included the effect of one previous choice (persistence parameter), but no multi-trial dependencies. It is hence possible that the differences in learning rate parameters between tasks were caused by differences in the bias induced by misspecification of history dependence, rather than a lack of generalization. Though pressing, however, this issue is difficult to resolve in practicality, because it is impossible to include all combinations of possible parameters in all computational models, i.e., to exhaustively search the space of possible models ("Every model is wrong, but to varying degrees"). Furthermore, even though our models were likely affected by some degree of misspecification, the research community is currently using models of this kind. Our study therefore sheds light on generalizability and interpretability in a realistic setting, which likely includes models with varying degrees of misspecification. Lastly, our models were fitted using robust computational tools and achieved good behavioral recovery (Fig. D.7), which also reduces the likelihood of model misspecification.“

2) Issue of reliability of parameter estimates

I think it is important to consider not only the bias in the parameter estimates, but also the issue of reliability, i.e., how stable the estimates will be when the same task is repeated with the same individual. For the task used in this study, has test-retest reliability been examined in previous studies? I think that parameters with low reliability will inevitably have low generalizability to other tasks. In this study, the use of three tasks seems to have addressed this issue without explicitly considering the reliability, but I would like the author to discuss this issue explicitly.

We thank the reviewer for this useful comment, and have added the following paragraph to the discussion section to address it:

“Furthermore, parameter generalizability is naturally bounded by parameter reliability, i.e., the stability of parameter estimates when participants perform the same task twice (test-retest reliability) or when estimating parameters from different subsets of the same dataset (split-half reliability). The reliability of RL models has recently become the focus of several parallel investigations [...], some employing very similar tasks to ours [...]. The investigations collectively suggest that excellent reliability can often be achieved with the right methods, most notably by using hierarchical model fitting. Reliability might still differ between tasks or models, potentially being lower for learning rates than other RL parameters [...], and differing between tasks (e.g., compare [...] to [...]). In this study, we used hierarchical fitting for tasks A and B and assessed a range of qualitative and quantitative measures of model fit for each task [...], boosting our confidence in high reliability of our parameter estimates, and the conclusion that the lack of between-task parameter correlations was not due to a lack of parameter reliability, but a lack of generalizability. This conclusion is further supported by the fact that larger between-task parameter correlations (r>0.5) than those observed in humans were attainable---using the same methods---in a simulated dataset with perfect generalization.“

3) About PCA

In this paper, principal component analysis (PCA) is used to extract common components from the parameter estimates and behavioral features across tasks. When performing PCA, were each parameter estimate and behavioral feature standardized so that the variance would be 1? There was no mention about this. It seems that otherwise the principal components would be loaded toward the features with larger variance. In addition, Moutoussis et al. (Neuron, 2021, 109 (12), 2025-2040) conducted a similar analysis of behavioral parameters of various decision-making tasks, but they used factor analysis instead of PCA. Although the authors briefly mentioned factor analysis, it would be better if they also mentioned the reason why they used PCA instead of factor analysis, which can consider unique variances.

To answer the reviewer's first question: We indeed standardized all features before performing the PCA. Apologies for missing to include this information - we have now added a corresponding sentence to the methods sections.

We also thank the reviewer for the mentioned reference, which is very relevant to our findings and can help explain the roles of different PCs. Like in our study, Moutoussis et al. found a first PC that captured variability in task performance, and subsequent PCs that captured task contrasts. We added the following paragraph to our manuscript:

“PC1 therefore captured a range of "good", task-engaged behaviors, likely related to the construct of "decision acuity" [...]. Like our PC1, decision acuity was the first component of a factor analysis (variant of PCA) conducted on 32 decision-making measures on 830 young people, and separated good and bad performance indices. Decision acuity reflects generic decision-making ability, and predicted mental health factors, was reflected in resting-state functional connectivity, but was distinct from IQ [...].”

To answer the reviewer's question about PCA versus FA, both approaches are relatively similar conceptually, and oftentimes share the majority of the analysis pipeline in practice. The main difference is that PCA breaks up the existing variance in a dataset in a new way (based on PCs rather than the original data features), whereas FA aims to identify an underlying model of latent factors that explain the observable features. This means that PCs are linear combinations of the original data features, whereas Factors are latent factors that give rise to the observable features of the dataset with some noise, i.e., including an additional error term.

However, in practice, both methods share the majority of computation in the way they are implemented in most standard statistical packages: FA is usually performed by conducting a PCA and then rotating the resulting solution, most commonly using the Varimax rotation, which maximizes the variance between features loadings on each factor in order to make the result more interpretable, and thereby foregoing the optimal solution that has been achieved by the PCA (which lack the error term). Maximum variance in feature loadings means that as many features as possible will have loadings close to 0 and 1 on each factor, reducing the number of features that need to be taken into account when interpreting this factor. Most relevant in our situation is that PCA is usually a special case of FA, with the only difference that the solution is not rotated for maximum interpretability. (Note that this rotation can be minor if feature loadings already show large variance in the PCA solution.)

To determine how much our results would change in practice if we used FA instead of PCA, we repeated the analysis using FA. Both are shown side-by-side below, and the results are quite similar:

We therefore conclude that our specific results are robust to the choice of method used, and that there is reason to believe that our PC1 is related to Moutoussis et al.’s F1 despite the differences in method.

Reviewer #2 (Public Review):

I am enthusiastic about the comprehensive approach, the thorough analysis, and the intriguing findings. This work makes a timely contribution to the field and warrants a wider discussion in the community about how computational methods are deployed and interpreted. The paper is also a great and rare example of how much can be learned from going beyond a meta-analytic approach to systematically collect data that assess commonly held assumptions in the field, in this case in a large data-driven study across multiple tasks. My only criticism is that at times, the paper misses opportunities to be more constructive in pinning down exactly why authors observe inconsistencies in parameter fits and interpretation. And the somewhat pessimistic outlook relies on some results that are, in my view at least, somewhat expected based on what we know about human RL. Below I summarize the major ways in which the paper's conclusions could be strengthened.

One key point the authors make concerns the generalizability of absolute vs. relative parameter values. It seems that at least in the parameter space defined by +LRs and exploration/noise (which are known to be mathematically coupled), subjects clustered similarly for tasks A and C. In other words, as the authors state, "both learning rate and inverse temperature generalized in terms of the relationships they captured between participants". This struck me as a more positive and important result than it was made out to be in the paper, for several reasons:

• As authors point out in the discussion, a large literature on variable LRs has shown that people adapt their learning rates trial-by-trial to the reward function of the environment; given this, and given that all models tested in this work have fixed learning rates, while the three tasks vary on the reward function, the comparison of absolute values seems a bit like a red-herring.

We thank the reviewers for this recommendation and have reworked the paper substantially to address the issue. We have modified the highlights, abstract, introduction, discussion, conclusion, and relevant parts of the results section to provide equal weight to the successes and failures of generalization.

Highlights:

● “RL decision noise/exploration parameters generalize in terms of between-participant variation, showing similar age trajectories across tasks.”

● “These findings are in accordance with previous claims about the developmental trajectory of decision noise/exploration parameters.”

Abstract:

● “We found that some parameters (exploration / decision noise) showed significant generalization: they followed similar developmental trajectories, and were reciprocally predictive between tasks.“

The introduction now introduces different potential outcomes of our study with more equal weight:

“Computational modeling enables researchers to condense rich behavioral datasets into simple, falsifiable models (e.g., RL) and fitted model parameters (e.g., learning rate, decision temperature) [...]. These models and parameters are often interpreted as a reflection of ("window into") cognitive and/or neural processes, with the ability to dissect these processes into specific, unique components, and to measure participants' inherent characteristics along these components.

For example, RL models have been praised for their ability to separate the decision making process into value updating and choice selection stages, allowing for the separate investigation of each dimension. Crucially, many current research practices are firmly based on these (often implicit) assumptions, which give rise to the expectation that parameters have a task- and model-independent interpretation and will seamlessly generalize between studies. However, there is growing---though indirect---evidence that these assumptions might not (or not always) be valid.

The following section lays out existing evidence in favor and in opposition of model generalizability and interpretability. Building on our previous opinion piece, which---based on a review of published studies---argued that there is less evidence for model generalizability and interpretability than expected based on current research practices [...], this study seeks to directly address the matter empirically.”

We now also provide more even evidence for both potential outcomes:

“Many current research practices are implicitly based on the interpretability and generalizability of computational model parameters (despite the fact that many researchers explicitly distance themselves from these assumptions). For our purposes, we define a model variable (e.g., fitted parameter, reward-prediction error) as generalizable if it is consistent across uses, such that a person would be characterized with the same values independent of the specific model or task used to estimate the variable. Generalizability is a consequence of the assumption that parameters are intrinsic to participants rather than task dependent (e.g., a high learning rate is a personal characteristic that might reflect an individual's unique brain structure). One example of our implicit assumptions about generalizability is the fact that we often directly compare model parameters between studies---e.g., comparing our findings related to learning-rate parameters to a previous study's findings related to learning-rate parameters. Note that such a comparison is only valid if parameters capture the same underlying constructs across studies, tasks, and model variations, i.e., if parameters generalize. The literature has implicitly equated parameters in this way in review articles [...], meta-analyses [...], and also most empirical papers, by relating parameter-specific findings across studies. We also implicitly evoke parameter generalizability when we study task-independent empirical parameter priors [...], or task-independent parameter relationships (e.g., interplay between different kinds of learning rates [...]), because we presuppose that parameter settings are inherent to participants, rather than task specific.

We define a model variable as interpretable if it isolates specific and unique cognitive elements, and/or is implemented in separable and unique neural substrates. Interpretability follows from the assumption that the decomposition of behavior into model parameters "carves cognition at its joints", and provides fundamental, meaningful, and factual components (e.g., separating value updating from decision making). We implicitly invoke interpretability when we tie model variables to neural substrates in a task-general way (e.g., reward prediction errors to dopamine function [...]), or when we use parameters as markers of psychiatric conditions (e.g., working-memory parameter and schizophrenia [...]). Interpretability is also required when we relate abstract parameters to aspects of real-world decision making [...], and generally, when we assume that model variables are particularly "theoretically meaningful" [...].

However, in midst the growing recognition of computational modeling, the focus has also shifted toward inconsistencies and apparent contradictions in the emerging literature, which are becoming apparent in cognitive [...], developmental [...], clinical [...], and neuroscience studies [...], and have recently become the focus of targeted investigations [...]. For example, some developmental studies have shown that learning rates increased with age [...], whereas others have shown that they decrease [...]. Yet others have reported U-shaped trajectories with either peaks [...] or troughs [...] during adolescence, or stability within this age range [...] (for a comprehensive review, see [...]; for specific examples, see [...]). This is just one striking example of inconsistencies in the cognitive modeling literature, and many more exist [...]. These inconsistencies could signify that computational modeling is fundamentally flawed or inappropriate to answer our research questions. Alternatively, inconsistencies could signify that the method is valid, but our current implementations are inappropriate [...]. However, we hypothesize that inconsistencies can also arise for a third reason: Even if both method and implementation are appropriate, inconsistencies like the ones above are expected---and not a sign of failure---if implicit assumptions of generalizability and interpretability are not always valid. For example, model parameters might be more context-dependent and less person-specific that we often appreciate [...]“

In the results section, we now highlight findings more that are compatible with generalization: “For α+, adding task as a predictor did not improve model fit, suggesting that α+ showed similar age trajectories across tasks (Table 2). Indeed, α+ showed a linear increase that tapered off with age in all tasks (linear increase: task A: β = 0.33, p < 0.001; task B: β = 0.052, p < 0.001; task C: β = 0.28, p < 0.001; quadratic modulation: task A: β = −0.007, p < 0.001; task B: β = −0.001, p < 0.001; task C: β = −0.006, p < 0.001). For noise/exploration and Forgetting parameters, adding task as a predictor also did not improve model fit (Table 2), suggesting similar age trajectories across tasks.”

“For both α+ and noise/exploration parameters, task A predicted tasks B and C, and tasks B and C predicted task A, but tasks B and C did not predict each other (Table 4; Fig. 2D), reminiscent of the correlation results that suggested successful generalization (section 2.1.2).”

“Noise/exploration and α+ showed similar age trajectories (Fig. 2C) in tasks that were sufficiently similar (Fig. 2D).” And with respect to our simulation analysis (for details, see next section):

“These results show that our method reliably detected parameter generalization in a dataset that exhibited generalization. ”

We also now provide more nuance in our discussion of the findings:

“Both generalizability [...] and interpretability (i.e., the inherent "meaningfulness" of parameters) [...] have been explicitly stated as advantages of computational modeling, and many implicit research practices (e.g., comparing parameter-specific findings between studies) showcase our conviction in them [...]. However, RL model generalizability and interpretability has so far eluded investigation, and growing inconsistencies in the literature potentially cast doubt on these assumptions. It is hence unclear whether, to what degree, and under which circumstances we should assume generalizability and interpretability. Our developmental, within-participant study revealed a nuanced picture: Generalizability and interpretability differed from each other, between parameters, and between tasks.”

“Exploration/noise parameters showed considerable generalizability in the form of correlated variance and age trajectories. Furthermore, the decline in exploration/noise we observed between ages 8-17 was consistent with previous studies [13, 66, 67], revealing consistency across tasks, models, and research groups that supports the generalizability of exploration / noise parameters. However, for 2/3 pairs of tasks, the degree of generalization was significantly below the level of generalization expected for perfect generalization. Interpretability of exploration / noise parameters was mixed: Despite evidence for specificity in some cases (overlap in parameter variance between tasks), it was missing in others (lack of overlap), and crucially, parameters lacked distinctiveness (substantial overlap in variance with other parameters).”

“Taken together, our study confirms the patterns of generalizable exploration/noise parameters and task-specific learning rate parameters that are emerging from the literature [13].”

• Regarding the relative inferred values, it's unclear how high we really expect correlations between the same parameter across tasks to be. E.g., if we take Task A and make a second, hypothetical, Task B by varying one feature at a time (say, stochasticity in reward function), how correlated are the fitted LRs going to be? Given the different sources of noise in the generative model of each task and in participant behavior, it is hard to know whether a correlation coefficient of 0.2 is "good enough" generalizability.

We thank the reviewer for this excellent suggestion, which we think helped answer a central question that our previous analyses had failed to address, and also provided answers to several other concerns raised by both reviewers in other section. We have conducted these additional analyses as suggested, simulating artificial behavioral data for each task, fitting these data using the models used in humans, repeating the analyses performed on humans on the new fitted parameters, and using bootstrapping to statistically compare humans to the hence obtained ceiling of generalization. We have added the following section to our paper, which describes the results in detail:

“Our analyses so far suggest that some parameters did not generalize between tasks, given differences in age trajectories (section 2.1.3) and a lack of mutual prediction (section 2.1.4). However, the lack of correspondence could also arise due to other factors, including behavioral noise, noise in parameter fitting, and parameter trade-offs within tasks. To rule these out, we next established the ceiling of generalizability attainable using our method.

We established the ceiling in the following way: We first created a dataset with perfect generalizability, simulating behavior from agents that use the same parameters across all tasks (suppl. Appendix E). We then fitted this dataset in the same way as the human dataset (e.g., using the same models), and performed the same analyses on the fitted parameters, including an assessment of age trajectories (suppl. Table E.8) and prediction between tasks (suppl. Tables E.9, E.10, and E.11). These results provide the practical ceiling of generalizability. We then compared the human results to this ceiling to ensure that the apparent lack of generalization was valid (significant difference between humans and ceiling), and not in accordance with generalization (lack of difference between humans and ceiling).

Whereas humans had shown divergent trajectories for parameter alpha- (Fig. 2B; Table 1), the simulated agents did not show task differences for alpha- or any other parameter (suppl. Fig E.8B; suppl. Table E.8, even when controlling for age (suppl. Tables E.9 and E.10), as expected from a dataset of generalizing agents. Furthermore, the same parameters were predictive between tasks in all cases (suppl. Table E.11). These results show that our method reliably detected parameter generalization in a dataset that exhibited generalization.

Lastly, we established whether the degree of generalization in humans was significantly different from agents. To this aim, we calculated the Spearman correlations between each pair of tasks for each parameter, for both humans (section 2.1.2; suppl. Fig. H.9) and agents, and compared both using bootstrapped confidence intervals (suppl. Appendix E). Human parameter correlations were significantly below the ceiling for all parameters except alpha+ (A vs B) and epsilon / 1/beta (A vs C; suppl. Fig. E.8C). This suggests that humans were within the range of maximally detectable generalization in two cases, but showed less-than-perfect generalization between other task combinations and for parameters Forgetting and alpha-.”

• The +LR/inverse temp relationship seems to generalize best between tasks A/C, but not B/C, a common theme in the paper. This does not seem surprising given that in A and C there is a key additional task feature over the bandit task in B -- which is the need to retain state-action associations. Whether captured via F (forgetting) or K (WM capacity), the cognitive processes involved in this learning might interact with LR/exploration in a different way than in a task where this may not be necessary.

We thank the reviewer for this comment, which raises an important issue. We are adding the specific pairwise correlations and scatter plots for the pairs of parameters the reviewer asked about below (“bf_alpha” = LR task A; “bf_forget” = F task A; “rl_forget” = F task C; “rl_log_alpha” = LR task C; “rl_K” = WM capacity task C):

Within tasks:

Between tasks:

To answer the question in more detail, we have expanded our section about limitations stemming from parameter tradeoffs in the following way:

“One limitation of our results is that regression analyses might be contaminated by parameter cross-correlations (sections 2.1.2, 2.1.3, 2.1.4), which would reflect modeling limitations (non-orthogonal parameters), and not necessarily shared cognitive processes. For example, parameters alpha and beta are mathematically related in the regular RL modeling framework, and we observed significant within-task correlations between these parameters for two of our three tasks (suppl. Fig. H.10, H.11). This indicates that caution is required when interpreting correlation results. However, correlations were also present between tasks (suppl. Fig. H.9, H.11), suggesting that within-model trade-offs were not the only explanation for shared variance, and that shared cognitive processes likely also played a role.

Another issue might arise if such parameter cross-correlations differ between models, due to the differences in model parameterizations across tasks. For example, memory-related parameters (e.g., F, K in models A and C) might interact with learning- and choice-related parameters (e.g., alpha+, alpha-, noise/exploration), but such an interaction is missing in models that do not contain memory-related parameters (e.g., task B). If this indeed the case, i.e., parameters trade off with each other in different ways across tasks, then a lack of correlation between tasks might not reflect a lack of generalization, but just the differences in model parameterizations. Suppl. Fig. \ref{figure:S2AlphaBetaCorrelations} indeed shows significant, medium-sized, positive and negative correlations between several pairs of Forgetting, memory-related, learning-related, and exploration parameters (though with relatively small effect sizes; Spearman correlation: 0.17 < |r| < 0.22).

The existence of these correlations (and differences in correlations between tasks) suggest that memory parameters likely traded off with each other, as well as with other parameters, which potentially affected generalizability across tasks. However, some of the observed correlations might be due to shared causes, such as a common reliance on age, and the regression analyses in the main paper control for these additional sources of variance, and might provide a cleaner picture of how much variance is actually shared between parameters.

Furthermore, correlations between parameters within models are frequent in the existing literature, and do not prevent researchers from interpreting parameters---in this sense, the existence of similar correlations in our study allows us to address the question of generalizability and interpretability in similar circumstances as in the existing literature.”

• More generally, isn't relative generalizability the best we would expect given systematic variation in task context? I agree with the authors' point that the language used in the literature sometimes implies an assumption of absolute generalizability (e.g. same LR across any task). But parameter fits, interactions, and group differences are usually interpreted in light of a single task+model paradigm, precisely b/c tasks vary widely across critical features that will dictate whether different algorithms are optimal or not and whether cognitive functions such as WM or attention may compensate for ways in which humans are not optimal. Maybe a more constructive approach would be to decompose tasks along theoretically meaningful features of the underlying Markov Decision Process (which gives a generative model), and be precise about (1) which features we expect will engage additional cognitive mechanisms, and (2) how these mechanisms are reflected in model parameters.

We thank the reviewer for this comment, and will address both points in turn:

(1) We agree with the reviewer's sentiment about relative generalizability: If we all interpreted our models exclusively with respect to our specific task design, and never expected our results to generalize to other tasks or models, there would not be a problem. However, the current literature shows a different pattern: Literature reviews, meta-analyses, and discussion sections of empirical papers regularly compare specific findings between studies. We compare specific parameter values (e.g., empirical parameter priors), parameter trajectories over age, relationships between different parameters (e.g., balance between LR+ and LR-), associations between parameters and clinical symptoms, and between model variables and neural measures on a regular basis. The goal of this paper was really to see if and to what degree this practice is warranted. And the reviewer rightfully alerted us to the fact that our data imply that these assumptions might be valid in some cases, just not in others.

(2) With regard to providing task descriptions that relate to the MDP framework, we have included the following sentence in the discussion section:

“Our results show that discrepancies are expected even with a consistent methodological pipeline, and using up-to-date modeling techniques, because they are an expected consequence of variations in experimental tasks and computational models (together called "context"). Future research needs to investigate these context factors in more detail. For example, which task characteristics determine which parameters will generalize and which will not, and to what extent? Does context impact whether parameters capture overlapping versus distinct variance? A large-scale study could answer these questions by systematically covering the space of possible tasks, and reporting the relationships between parameter generalizability and distance between tasks. To determine the distance between tasks, the MDP framework might be especially useful because it decomposes tasks along theoretically meaningful features of the underlying Markov Decision Process.“

Another point that merits more attention is that the paper pretty clearly commits to each model as being the best possible model for its respective task. This is a necessary premise, as otherwise, it wouldn't be possible to say with certainty that individual parameters are well estimated. I would find the paper more convincing if the authors include additional information and analysis showing that this is actually the case.

We agree with the sentiment that all models should fit their respective task equally well. However, there is no good quantitative measure of model fit that is comparable across tasks and models - for example, because of the difference in difficulty between the tasks, the number of choices explained would not be a valid measure to compare how well the models are doing across tasks. To address this issue, we have added the new supplemental section (Appendix C) mentioned above that includes information about the set of models compared, and explains why we have reason to believe that all models fit (equally) well. We also created the new supplemental Figure D.7 shown above, which directly compares human and simulated model behavior in each task, and shows a close correspondence for all tasks. Because the quality of all our models was a major concern for us in this research, we also refer the reviewer and other readers to the three original publications that describe all our modeling efforts in much more detail, and hopefully convince the reviewer that our model fitting was performed according to high standards.

I am particularly interested to see whether some of the discrepancies in parameter fits can be explained by the fact that the model for Task A did not account for explicit WM processes, even though (1) Task A is similar to Task C (Task A can be seen as a single condition of Task C with 4 states and 2 possible visible actions, and stochastic rather than deterministic feedback) and (2) prior work has suggested a role for explicit memory of single episodes even in stateless bandit tasks such as Task B.

We appreciate this very thoughtful question, which raises several important issues. (1) As the reviewer said, the models for task A and task C are relatively different even though the underlying tasks are relatively similar (minus the differences the reviewer already mentioned, in terms of visibility of actions, number of actions, and feedback stochasticity). (2) We also agree that the model for task C did not include episodic memory processes even though episodic memory likely played a role in this task, and agree that neither the forgetting parameters in tasks A and C, nor the noise/exploration parameters in tasks A, B, and C are likely specific enough to capture all the memory / exploration processes participants exhibited in these tasks.

However, this problem is difficult to solve: We cannot fit an episodic-memory model to task B because the task lacks an episodic-memory manipulation (such as, e.g., in Bornstein et al., 2017), and we cannot fit a WM model to task A because it lacks the critical set-size manipulation enabling identification of the WM component (modifying set size allows the model to identify individual participants’ WM capacities, so the issue cannot be avoided in tasks with only one set size). Similarly, we cannot model more specific forgetting or exploration processes in our tasks because they were not designed to dissociate these processes. If we tried fitting more complex models that include these processes to these tasks, they would most likely lose in model comparison because the increased complexity would not lead to additional explained behavioral variance, given that the tasks do not elicit the relevant behavioral patterns. Because the models therefore do not specify all the cognitive processes that participants likely employ, the situation described by the reviewer arises, namely that different parameters sometimes capture the same cognitive processes across tasks and models, while the same parameters sometimes capture different processes.

And while the reviewer focussed largely on memory-related processes, the issue of course extends much further: Besides WM, episodic memory, and more specific aspects of forgetting and exploration, our models also did not take into account a range of other processes that participants likely engaged in when performing the tasks, including attention (selectivity, lapses), reasoning / inference, mental models (creation and use), prediction / planning, hypothesis testing, etc., etc. In full agreement with the reviewer’s sentiment, we recently argued that this situation is ubiquitous to computational modeling, and should be considered very carefully by all modelers because it can have a large impact on model interpretation (Eckstein et al., 2021).

If we assume that many more cognitive processes are likely engaged in each task than are modeled, and consider that every computational model includes just a small number of free parameters, parameters then necessarily reflect a multitude of cognitive processes. The situation is additionally exacerbated by the fact that more complex models become increasingly difficult to fit from a methodological perspective, and that current laboratory tasks are designed in a highly controlled and consequently relatively simplistic way that does not lend itself to simultaneously test a variety of cognitive processes.

The best way to deal with this situation, we think, is to recognize that in different contexts (e.g., different tasks, different computational models, different subject populations), the same parameters can capture different behaviors, and different parameters can capture the same behaviors, for the reasons the reviewer lays out. Recognizing this helps to avoid misinterpreting modeling results, for example by focusing our interpretation of model parameters to our specific task and model, rather than aiming to generalize across multiple tasks. We think that recognizing this fact also helps us understand the factors that determine whether parameters will capture the same or different processes across contexts and whether they will generalize. This is why we estimated here whether different parameters generalize to different degrees, which other factors affect generalizability, etc. Knowing the practical consequences of using the kinds of models we currently use will therefore hopefully provide a first step in resolving the issues the reviewer laid out.

It is interesting that one of the parameters that generalizes least is LR-. The authors make a compelling case that this is related to a "lose-stay" behavior that benefits participants in Task B but not in Task C, which makes sense given the probabilistic vs deterministic reward function. I wondered if we can rule out the alternative explanation that in Task C, LR- could reflect a different interpretation of instructions vis. a vis. what rewards indicate - do authors have an instruction check measure in either task that can be correlated with this "lose-stay" behavior and with LR-? And what does the "lose-stay" distribution look like, for Task C at least? I basically wonder if some of these inconsistencies can be explained by participants having diverging interpretations of the deterministic nature of the reward feedback in Task C. The order of tasks might matter here as well -- was task order the same across participants? It could be that due to the within-subject design, some participants may have persisted in global strategies that are optimal in Task B, but sub-optimal in Task C.

The PCA analysis adds an interesting angle and a novel, useful lens through which we can understand divergence in what parameters capture across different tasks. One observation is that loadings for PC2 and PC3 are strikingly consistent for Task C, so it looks more like these PCs encode a pairwise contrast (PC2 is C with B and PC2 is C with A), primarily reflecting variability in performance - e.g. participants who did poorly on Task C but well on Task B (PC2) or Task A (PC3). Is it possible to disentangle this interpretation from the one in the paper? It also is striking that in addition to performance, the PCs recover the difference in terms of LR- on Task B, which again supports the possibility that LR- divergence might be due to how participants handle probabilistic vs. deterministic feedback.

We appreciate this positive evaluation of our PCA and are glad that it could provide a useful lens for understanding parameters. We also agree to the reviewer's observation that PC2 and PC3 reflect task contrasts (PC2: task B vs task C; PC3: task A vs task C), and phrase it in the following way in the paper:

“PC2 contrasted task B to task C (loadings were positive / negative / near-zero for corresponding features of tasks B / C / A; Fig. 3B). PC3 contrasted task A to both B and C (loadings were positive / negative for corresponding features on task A / tasks B and C; Fig. 3C).”

Hence, the only difference between our interpretation and the reviewer’s seems to be whether PC3 contrasts task C to task B as well as task A, or just to task A. Our interpretation is supported by the fact that loadings for tasks A and C are quite similar on PC3; however, both interpretations seem appropriate.

We also appreciate the reviewer's positive evaluation of the fact that the PCA reproduces the differences in LR-, and its relationship to probabilistic/deterministic feedback. The following section reiterates this idea:

“alpha- loaded positively in task C, but negatively in task B, suggesting that performance increased when participants integrated negative feedback faster in task C, but performance decreased when they did the same in task B. As mentioned before, contradictory patterns of alpha- were likely related to task demands: The fact that negative feedback was diagnostic in task C likely favored fast integration of negative feedback, while the fact that negative feedback was not diagnostic in task B likely favored slower integration (Fig. 1E). This interpretation is supported by behavioral findings: "Lose-stay" behavior (repeating choices that produce negative feedback) showed the same contrasting pattern as alpha- on PC1. It loaded positively in task B, showing Lose-stay behavior benefited performance, but it loaded negatively on task C, showing that it hurt performance (Fig. 3A). This supports the claim that lower alpha- was beneficial in task B, while higher alpha- was beneficial in task C, in accordance with participant behavior and developmental differences.“

Author Response

Reviewer #1 (Public Review):

Bice et al. present new work using an optogenetics-based stimulation to test how this affects stroke recovery in mice. Namely, can they determine if contralateral stimulation of S1 would enhance or hinder recovery after a stroke? The study provides interesting evidence that this stimulation may be harmful, and not helpful. They found that contralesional optogenetic-based excitation suppressed perilesional S1FP remapping, and this caused abnormal patterns of evoked activity in the unaffected limb. They applied a network analysis framework and found that stimulation prevented the restoration of resting-state functional connectivity within the S1FP network, and resulted in limb-use asymmetry in the mice. I think it's an important finding. My suggestions for improvement revolve around quantitative analysis of the behavior, but the experiments are otherwise convincing and important.

Thank you for the positive feedback regarding our work.

Other comments - Data and paper presentation:

1) Figure 1A is misleading; it appears as if optogenetic stimulation is constant (which indeed would be detrimental to the tissue). Also, the atlas map overlaps color-wise with conditions; at a glance it looks like the posterior cortex might be stimulated; consider making greyscale?

We have updated Figure 1A to address these concerns.

Reviewer #2 (Public Review):

These studies test the effect of stimulation of the contralateral somatosensory cortex on recovery, evoked responses, functional interconnectivity and gene expression in a somatosensory cortex stroke. Using transgenic mice with ChR2 in excitatory neurons, these neurons are stimulated in somatosensory cortex from days 1 after stroke to 4 weeks. This stimulation is fairly brief: 3min/day. Mice then received behavioral analysis, electrical forepaw stimulation and optical intrinsic signal mapping, and resting state MRI. The core finding is that this ChR2 stimulation of excitatory neurons in contralateral somatosensory cortex impairs recovery, evoked activity and interconnectivity of contralateral (to the stimulation, ipsilateral to the stroke) cortex in this localized stroke model. This is a surprising result, and resonates with some clinical findings, and a robust clinical discussion, on the role of the contralateral cortex in recovery. This manuscript addresses several important topics. The issue of brain stimulation and alterations in brain activity that the studies explore are also part of human brain stimulation protocols, and pre-clinical studies. The finding that contralateral stimulation inhibits recovery and functional circuit remapping is an important one. The rsMRI analysis is sophisticated.

Thank you for the supportive comments regarding our manuscript

Concerns:

1) The gene expression data is to be expected. Stimulation of the brain in almost any context alters the expression of genes.

We agree with the reviewer that stimulation of the brain is expected to broadly alter gene expression. However, in this set of studies, we examined a subset of genes that are of particular interest in neuroplasticity, and compared expression in ipsi-lesional vs. contra-lesional cortex in the presence or absence of contralesional stimulation during the post stroke recovery period. Genes like Arc, for example, have been shown by our group to be necessary for perilesional plasticity and recovery (Kraft, et al., Science Translational Medicine, 2018). The finding that validated plasticity genes are suppressed by contralesional stimulation is consistent with the central finding that contralesional stimulation suppresses the recovery of normal patterns of brain organization and activity. Importantly, there were also genes associated with spontaneous recovery that were unaltered or increased by contra-lesional brain stimulation. While these data do not provide causal associations, they may prove to be useful for developing hypotheses regarding molecular mechanisms involved in spontaneous brain repair for future studies.

In light of the reviewer’s comment, we have altered text throughout to not focus on specific directionality of transcripts. Instead, we indicate that relevant transcript changes are those that are altered in association with spontaneous recovery, and which are altered in the opposite direction with contralesional brain stimulation.

Minor points.

1) Was the behavior and the functional imaging done while the brain was being stimulated?

We have updated the methods (page 17) to clarify that the only experiments during which the photostimulus occurred during neuroimaging are reported in new Figure 6, and to clarify that photostimulation did not occur during the behavioral tests of asymmetry.

2) It would be useful to understand what is being stimulated. The stimulation method is not described. Is an entire cortical width of tissue stimulated, and this is what is feeding back onto the contralateral cortex? Or is this stimulation mostly affecting excitatory (CaMKII+) cells in upper or lower layers? This will be important to be able to compare to the Chen et al study that gave rise to the stimulation approach here. This gets to the issue of the circuitry that is important in recovery, or in inhibiting recovery. One might answer this question by doing the stimulation and staining tissue for immediate early gene activation, to see the circuits with evoked activity. Also, the techniques used in this study could be applied with OIS or rsMRI during stimulation, to determine the circuits that are activated.

We have clarified the stimulation protocol in response to Essential point 2.2. Due to light scattering and appreciable attenuation of 473nm in brain tissue, only ~1% of photons penetrate to a depth of 600 microns. Experimentally, this provides superficial-layer specificity to Layer 2/3 Camk2a cells (https://doi.org/10.1016/j.neuron.2011.06.004)

To answer the question of what circuits are affecting recovery, we performed 2 sets of additional experiments – Experiment 1: OISI during photostimulation before and after photothrombosis, and Experiment 2: tissue staining for IEG expression (cFOS). We describe each below:

Experiment 1 New results are included from 16 Camk2a-ChR2 mice (Results, page 10-11; Methods, page 18) and reported as new Figure 6. Similar to the previously reported experiments, all mice were subject to photothrombosis of left S1FP, half of which received interventional optogenetic photostimulation beginning 1 day after photothrombosis (+Stim) while the other half recovered spontaneously (-Stim). To visualize in real time whether contralesional photostimulation differentially affected global cortical activity in these 2 groups, concurrent awake OISI during acute contralesional photostimulation was performed in +Stim and –Stim groups before, 1, and 4 weeks after photothrombosis. At baseline, all mice exhibited focal increases in right S1FP activity during photostimulation that spread to contralateral (left) S1FP and other motor regions approximately 8-10 seconds after stimulus onset. While activity increases within the targeted circuit, subtle inhibition of cortical activity can also be observed in surrounding non-targeted cortices. Thus, activity both increases and decreases in different cortical regions during and after optogenetic stimulation of the right S1FP circuit. Of note, regions that are inhibited by S1FP stimulation show more pronounced decreases in activity in +Stim mice at 1 and 4 weeks compared to baseline and were significantly larger in +Stim mice compared to –Stim mice. We conclude that focal stimulation of contralesional cortex results in significant, widespread inhibitory influences that extend well beyond the targeted circuit.

Experiment 2 For experiment 2, we hypothesized that IEG expression would increase in photostimulated regions, cortical regions functionally connected to targeted areas, and potentially deeper brain regions. For the IEG experiments, healthy ChR2 naïve animals (C57 mice) or CamK2a-ChR2 mice were acclimated to the head-restraint apparatus described in the manuscript used for photostimulation treatment. Once trained, awake mice were subject to the same photostimulus protocol as described in the manuscript applied to forepaw somatosensory cortex in the right hemisphere. After stimulation, mice were sacrificed, perfused, and brains were harvested for tissue slicing and immunostaining for cFOS. Tissue slices containing right and left primary forepaw somatosensory cortex and primary and secondary motor cortices (+0.5mm A/P) or visual cortex (-2.8mm A/P) were examined for cFOS staining and compared across groups.

Below is a summary table of our findings, and representative tissue slices. While c-FOS IHC was successful, results are not consistent with expectations from the mouse strains used. Only 1 ChR2+ mouse exhibited staining patterns consistent with local S1FP photostimulation, while expression in ChR2- mice was more variable, and in some instances exhibits higher expression in targeted circuits compared to ChR2+ mice. It is possible that awake behaving mice already exhibit high activity in sensorimotor cortex at rest, which might obscure changes specific to optogenetic photostimulation. Regardless, because the tissue staining experiments were inconclusive in healthy animals, we did not proceed with further experiments in the stroke groups, and do not report these findings in the manuscript.

3) Also, it is possible that contralateral stimulation is impairing recovery, not through an effect on the contralateral cortex (the site of the stroke), but on descending projections, or theoretically even through evoking activity or subclinical movement of the contralateral limb (ipsilateral to the stroke). By more carefully mapping the distribution of the activity of the stimulated brain region, and what exactly is being stimulated, these issues can be explored.

The reviewer raises an excellent point. We have added to the “Limitations and Future work” section of the Discussion on pages 15-16

Author Response

Reviewer #1 (Public Review):

It is now widely accepted that the age of the brain can differ from the person's chronological age and neuroimaging methods are ideally suited to analyze the brain age and associated biomarkers. Preclinical studies of rodent models with appropriate neuroimaging do attest that lifestyle-related prevention approaches may help to slow down brain aging and the potential of BrainAGE as a predictor of age-related health outcomes. However, there is a paucity of data on this in humans. It is in this context the present manuscript receives its due attention.

Comments:

1) Lifestyle intervention benefits need to be analyzed using robust biomarkers which should be profiled non-invasively in a clinical setting. There is increasing evidence of the role of telomere length in brain aging. Gampawar et al (2020) have proposed a hypothesis on the effect of telomeres on brain structure and function over the life span and named it as the "Telomere Brain Axis". In this context, if the authors could measure telomere length before and after lifestyle intervention, this will give a strong biomarker utility and value addition for the lifestyle modification benefits. 2) Authors should also consider measuring BDNF levels before and after lifestyle intervention.

Response to comments 1+2: we agree that associating both telomere length and BDNF level with brain age would be interesting and relevant. However, we did not measure these two variables. We would certainly consider adding these in future work. Regarding telomere length, we now include a short discussion of brain age in relation to other bodily ages, such as telomere length (Discussion section):

“Studying changes in functional brain aging is part of a broader field that examines changes in various biological ages, such as telomere length1, DNA methylation2, and arterial stiffness3. Evaluating changes in these bodily systems over time allows us to capture health and lifestyle-related factors that affect overall aging and may guide the development of targeted interventions to reduce age-related decline. For example, in the CENTRAL cohort, we recently reported that reducing body weight and intrahepatic fat following a lifestyle intervention was related to methylation age attenuation4. In the current work, we used RSFC for brain age estimation, which resulted in a MAE of ~8 years, which was larger than the intervention period. Nevertheless, we found that brain age attenuation was associated with changes in multiple health factors. The precision of an age prediction model based on RSFC is typically lower than a model based on structural brain imaging5. However, a higher model precision may result in a lower sensitivity to detect clinical effects6,7. Better tools for data harmonization among dataset6 and larger training sample size5 may improve the accuracy of such models in the future. We also suggest that examining the dynamics of multiple bodily ages and their interactions would enhance our understanding of the complex aging process8,9. “

And

“These findings complement the growing interest in bodily aging indicated, for example, by DNA methylation4 as health biomarkers and interventions that may affect them.”

Reviewer #2 (Public Review):

In this study, Levakov et al. investigated brain age based on resting-state functional connectivity (RSFC) in a group of obese participants following an 18-month lifestyle intervention. The study benefits from various sophisticated measurements of overall health, including body MRI and blood biomarkers. Although the data is leveraged from a solid randomized control set-up, the lack of control groups in the current study means that the results cannot be attributed to the lifestyle intervention with certainty. However, the study does show a relationship between general weight loss and RSFC-based brain age estimations over the course of the intervention. While this may represent an important contribution to the literature, the RSFC-based brain age prediction shows low model performance, making it difficult to interpret the validity of the derived estimates and the scale of change. The study would benefit from more rigorous analyses and a more critical discussion of findings. If incorporated, the study contributes to the growing field of literature indicating that weight-reduction in obese subjects may attenuate the detrimental effect of obesity on the brain.

The following points may be addressed to improve the study:

Brain age / model performance:

1) Figure 2: In the test set, the correlation between true and predicted age is 0.244. The fitted slope looks like it would be approximately 0.11 (55-50)/(80-35); change in y divided by change in x. This means that for a chronological age change of 12 months, the brain age changes by 0.11*12 = 1.3 months. I.e., due to the relatively poor model performance, an 80-year-old participant in the plot (fig 2) has a predicted age of ~55. Hence, although the age prediction step can generate a summary score for all the RSFC data, it can be difficult to interpret the meaning of these brain age estimates and the 'expected change' since the scale is in years.

2) In Figure 2 it could also help to add the x = y line to get a better overview of the prediction variance. The estimates are likely clustered around the mean/median age of the training dataset, and age is overestimated in younger subs and overestimated in older subs (usually referred to as "age bias"). It is important to inspect the data points here to understand what the estimates represent, i.e., is variation in RSFC potentially lost by wrapping the data in this summary measure, since the age prediction is not particularly accurate, and should age bias in the predictions be accounted for by adjusting the test data for the bias observed in the training data?

Response to comment 1+2: we agree with the reviewer that due to the relatively moderate correlation between the predicted and observed age, a large change in the observed age corresponds to a small change in the predicted age. We now state this limitation in Results section 2.1:

“Despite being significant and reproducible, we note that the correlations between the observed and predicted age were relatively moderate.”

And discuss this point in the Discussion section:

“In the current work, we used RSFC for brain age estimation, which resulted in a MAE of ~8 years, which was larger than the intervention period. Nevertheless, we found that brain age attenuation was associated with changes in multiple health factors. The precision of an age prediction model based on RSFC is typically lower than a model based on structural brain imaging5. However, a higher model precision may result in a lower sensitivity to detect clinical effects6,7. Better tools for data harmonization among dataset6 and larger training sample size5 may improve the accuracy of such models in the future.”

Moreover, , we now add the x=y line to Fig. 2, so the readers can better assess the prediction variance as suggested by the reviewer:

We prefer to avoid using different scales (year/month) in the x and y axes to avoid misleading the readers, but the list of observed and predicted ages are available as SI files with a precision of 2 decimals point (~3 days).

We note that despite the moderate precision accuracy, we replicated these results in three separate cohorts.

Regarding the effect of “age bias” (also known as “regression attenuation” or “regression dilution” 10), we are aware of this phenomenon and agree that it must be accounted for. In fact, the “age bias” is one of the reasons we chose to use the difference between the expected and observed ages as the primary outcome of the study, as this measure already takes this bias into account. To demonstrate this effect we now compute brain age attenuation in two ways: 1. As described and used in the current study (Methods 4.9); and 2. By regressing out the effect of age on the predicted brain age at both times separately, then subtracting the adjusted predicted age at T18 from the adjusted predicted age at T0. The second method is the standard method to account for age bias as described in a previous work 11. Below is a scatter plot of both measures across all participants:

The x-axis represents the first method, used in the current study, and the y-axis represents the second method, described in Smith et al., (2019). Across all subjects, we found a nearly perfect 1:1 correspondence between the two methods (r=.998, p<0.001; MAE=0.45), as the two are mathematically identical. The small gap between the two is because the brain age attenuation model also takes into account the difference in the exact time that passed between the two scans for each participant (mean=21.36m, std = 1.68m).

We now note this in Methods section 4.9:

“We note that the result of computing the difference between the bias-corrected brain age gap at both times was nearly identical to the brain age attenuation measure (r=.99, p<0.001; MAE=0.45). The difference between the two is because the brain age attenuation model takes into account the difference in the exact time that passed between the two scans for each participant (mean=21.36m, std = 1.68m).”

3) In Figure 3, some of the changes observed between time points are very large. For example, one subject with a chronological age of 62 shows a ten-year increase in brain age over 18 months. This change is twice as large as the full range of age variation in the brain age estimates (average brain age increases from 50 to 55 across the full chronological age span). This makes it difficult to interpret RSFC change in units of brain age. E.g., is it reasonable that a person's brain ages by ten years, either up or down, in 18 months? The colour scale goes from -12 years to 14 years, so some of the observed changes are 14 / 1.5 = 9 times larger than the actual time from baseline to follow-up.

• The questions above should be investigated and addressed in the context of potential challenges with using brain age as a marker (see e.g., https://onlinelibrary.wiley.com/doi/full/10.1002/hbm.25837, https://onlinelibrary.wiley.com/doi/full/10.1002/hbm.26144).

We agree that our model precision was relatively low, especially compared to the period of the intervention, as also stated by reviewer #1. We now discuss this issue in light of the studies pointed out by the reviewer (Discussion section):

“In the current work, we used RSFC for brain age estimation, which resulted in a MAE of ~8 years, which was larger than the intervention period. Nevertheless, we found that brain age attenuation was associated with changes in multiple health factors. The precision of an age prediction model based on RSFC is typically lower than a model based on structural brain imaging5. However, a higher model precision may result in a lower sensitivity to detect clinical effects6,7. Better tools for data harmonization among datasets6 and larger training sample size5 may improve the accuracy of such models in the future.”

Again, we note that despite the moderate precision accuracy, we replicated these results in three separate cohorts and found that both the correlation and the MAE between the predicted and observed age were significant in all of them.

RSFC for age prediction:

1) Several studies show better age prediction accuracy with structural MRI features compared to RSFC. If the focus of the study is to use an accurate estimate of brain ageing rather than specifically looking at changes in RSFC, adding structural MRI data could be helpful.

We focused on brain structural changes in a previous work, and the focus of the current work was assessing age-related functional connectivity alterations. We now added a few sentences in the Introduction section that would hopefully better motivate our choice:

“We previously found that weight loss, glycemic control, lowering of blood pressure, and increment in polyphenols-rich food were associated with an attenuation in brain atrophy 12. Obesity is also manifested in age-related changes in the brain’s functional organization as assessed with resting-state functional connectivity (RSFC). These changes are dynamic13 and can be observed in short time scales14 and thus of relevance when studying lifestyle intervention.”

2) If changes in RSFC are the main focus, using brain age adds a complicated layer that is not necessarily helpful. It could be easier to simply assess RSFC change from baseline to follow up, and correlate potential changes with changes in e.g., BMI.

We are specifically interested in age-related changes as we described a-priori in the registration of the study: https://clinicaltrials.gov/ct2/show/NCT03020186

Moreover, age-related changes in RSFC are complex, multivariate and dependent upon the choice of theoretical network measures. We think that a data-driven brain age prediction approach might better capture these multifaceted changes and their relation to aging. We now state this in the Introduction section:

“Studies have linked obesity with decreased connectivity within the default mode network15,16 and increased connectivity with the lateral orbitofrontal cortex17, which are also seen in normal aging18,19. Longitudinal trials have reported changes in these connectivity patterns following weight reduction20,21, indicating that they can be altered. However, findings regarding functional changes are less consistent than those related to anatomical changes due to the multiple measures22 and scales23 used to quantify RSFC. Hence, focusing on a single measure, the functional brain age, may better capture these complex, multivariant changes and their relation to aging. “

The lack of control groups

1) If no control group data is available, it is important to clarify this in the manuscript, and evaluate which conclusions can and cannot be drawn based on the data and study design.

We agree that this point should be made more clear, and we now state this in the limitation section of the Discussion:

“We also note that the lack of a no-intervention control group limits our ability to directly relate our findings to the intervention. Hence, we can only relate brain age attenuation to the observed changes in health biomarkers.”

Also, following reviewers’ #2 and #3 comments, we refer to the weight loss following 18 months of lifestyle intervention instead of to the intervention itself. This is now made clear in the title, abstract, and the main text.

Reviewer #3 (Public Review):

The authors report on an interesting study that addresses the effects of a physical and dietary intervention on accelerated/decelerated brain ageing in obese individuals. More specifically, the authors examined potential associations between reductions in Body-Mass-Index (BMI) and a decrease in relative brain-predicted age after an 18-months period in N = 102 individuals. Brain age models were based on resting-state functional connectivity data. In addition to change in BMI, the authors also tested for associations between change in relative brain age and change in waist circumference, six liver markers, three glycemic markers, four lipid markers, and four MRI fat deposition measures. Moreover, change in self-reported consumption of food, stratified by categories such as 'processed food' and 'sweets and beverages', was tested for an association with change in relative brain age. Their analysis revealed no evidence for a general reduction in relative brain age in the tested sample. However, changes in BMI, as well as changes in several liver, glycemic, lipid, and fat-deposition markers showed significant covariation with changes in relative brain age. Three markers remained significant after additionally controlling for BMI, indicating an incremental contribution of these markers to change in relative brain age. Further associations were found for variables of subjective food consumption. The authors conclude that lifestyle interventions may have beneficial effects on brain aging.

Overall, the writing is concise and straightforward, and the langue and style are appropriate. A strength of the study is the longitudinal design that allows for addressing individual accelerations or decelerations in brain aging. Research on biological aging parameters has often been limited to cross-sectional analyses so inferences about intra-individual variation have frequently been drawn from inter-individual variation. The presented study allows, in fact, investigating within-person differences. Moreover, I very much appreciate that the authors seek to publish their code and materials online, although the respective GitHub project page did not appear to be set to 'public' at the time (error 404). Another strength of the study is that brain age models have been trained and validated in external samples. One further strength of this study is that it is based on a registered trial, which allows for the evaluation of the aims and motivation of the investigators and provides further insights into the primary and secondary outcomes measures (see the clinical trial identification code).

One weakness of the study is that no comparison between the active control group and the two experimental groups has been carried out, which would have enabled causal inferences on the potential effects of different types of interventions on changes in relative brain age. In this regard, it should also be noted that all groups underwent a lifestyle intervention. Hence, from an experimenter's perspective, it is problematic to conclude that lifestyle interventions may modulate brain age, given the lack of a control group without lifestyle intervention. This issue is fueled by the study title, which suggests a strong focus on the effects of lifestyle intervention. Technically, however, this study rather constitutes an investigation of the effects of successful weight loss/body fat reduction on brain age among participants who have taken part in a lifestyle intervention. In keeping with this, the provided information on the main effect of time on brain age is scarce, essentially limited to a sign test comparing the proportions of participants with an increase vs. decrease in relative brain age. Interestingly, this analysis did not suggest that the proportion of participants who benefit from the intervention (regarding brain age) significantly exceeds the number of participants who do not benefit. So strictly speaking, the data rather indicates that it's not the lifestyle intervention per sé that contributes to changes in brain age, but successful weight loss/body fat reduction. In sum, I feel that the authors' claims on the effects of the intervention cannot be underscored very well given the lack of a control group without lifestyle intervention.

We agree that this point, also raised by reviewer #2, should be made clear, and we now state this in the limitation section of the Discussion:

“We also note that the lack of a no-intervention control group limits our ability to directly relate our findings to the intervention. Hence, we can only relate brain age attenuation to the observed changes in health biomarkers.”

Also, following reviewers #2 and #3, we refer to the weight loss following 18 months of lifestyle intervention instead of to the intervention itself. This is now explicitly mentioned in the title, abstract, and within the text:

Title: “The effect of weight loss following 18 months of lifestyle intervention on brain age assessed with resting-state functional connectivity”

Abstract: “…, we tested the effect of weight loss following 18 months of lifestyle intervention on predicted brain age, based on MRI-assessed resting-state functional connectivity (RSFC).”

Another major weakness is that no rationale is provided for why the authors use functional connectivity data instead of structural scans for their age estimation models. This gets even more evident in view of the relatively low prediction accuracies achieved in both the validation and test sets. My notion of the literature is that the vast majority of studies in this field implicate brain age models that were trained on structural MRI data, and these models have achieved way higher prediction accuracies. Along with the missing rationale, I feel that the low model performances require some more elaboration in the discussion section. To be clear, low prediction accuracies may be seen as a study result and, as such, they should not be considered as a quality criterion of the study. Nevertheless, the choice of functional MRI data and the relevance of the achieved model performances for subsequent association analysis needs to be addressed more thoroughly.

We agree that age estimation from structural compared to functional imaging yields a higher prediction accuracy. In a previous publication using the same dataset12, we demonstrated that weight loss was associated with an attenuation in brain atrophy, as we describe in the introduction:

“We previously found that weight loss, glycemic control and lowering of blood pressure, as well as increment in polyphenols rich food, were associated with an attenuation in brain atrophy 12.”

Here we were specifically interested in age-related functional alterations that are associated with successful weight reduction. Compared to structural brain changes aging effect on functional connectivity is more complex and multifaced. Hence, we decided to utilize a data-driven or prediction-driven approach for assessing age-related changes in functional connectivity by predicting participants’ functional brain age. We now describe this rationale in the introduction section:

“Studies have linked obesity with decreased connectivity within the default mode network15,16 and increased connectivity with the lateral orbitofrontal cortex17, which are also seen in normal aging18,19. Longitudinal trials have reported changes in these connectivity patterns following weight reduction20,21, indicating that they can be altered. However, findings regarding functional changes are less consistent than those related to anatomical changes due to the multiple measures22 and scales23 used to quantify RSFC. Hence, focusing on a single measure, the functional brain age, may better capture these complex changes and their relation to aging.”

We address the point regarding the low model performance in response to reviewer #2, comment #2.

Author Response:

Evaluation Summary:

The authors studied the neural correlates of planning and execution of single finger presses in a 7T fMRI study focusing on primary somatosensory (S1) and motor (M1) cortices. BOLD patterns of activation/deactivation and finger-specific pattern discriminability indicate that M1 and S1 are involved not only during execution, but also during planning of single finger presses. These results contribute to a developing story that the role of primary somatosensory cortex goes beyond pure processing of tactile information and will be of interest for researchers in the field of motor control and of systems neuroscience.