Reviewer #1 (Public review):

Summary:

Boldt et al test several possible relationships between trandiagnostically-defined compulsivity and cognitive offloading in a large online sample. To do so, they develop a new and useful cognitive task to jointly estimate biases in confidence and reminder-setting. In doing so, they find that over-confidence is related to less utilization of reminder-setting, which partially mediates the negative relationship between compulsivity and lower reminder-setting. The paper thus establishes that, contrary to the over-use of checking behaviors in patients with OCD, greater levels of transdiagnostically-defined compulsivity predicts less deployment of cognitive offloading. The authors offer speculative reasons as to why (perhaps it's perfectionism in less clinically-severe presentations that lowers the cost of expending memory resources), and sets an agenda to understand the divergence in cognitive between clinical and nonclinical samples. Because only a partial mediation had robust evidence, multiple effects may be at play, whereby compulsivity impacts cognitive offloading via overconfidence and also by other causal pathways.

Strengths:

The study develops an easy-to-implement task to jointly measure confidence and replicates several major findings on confidence and cognitive offloading. The study uses a useful measure of cognitive offloading - the tendency to set reminders to augment accuracy in the presence of experimentally manipulated costs. Moreover, the utilizes multiple measures of presumed biases -- overall tendency to set reminders, the empirically estimated indifference point at which people engage reminders, and a bias measure that compares optimal indifference points to engage reminders relative to the empirically observed indifference points. That the study observes convergenence along all these measures strengthens the inferences made relating compulsivity to the under-use of reminder-setting. Lastly, the study does find evidence for one of several a priori hypotheses and sets a compelling agenda to try to explain why such a finding diverges from an ostensible opposing finding in clinical OCD samples and the over-use of cognitive offloading.

Weaknesses:

Although I think this design and study are very helpful for the field, I felt that a feature of the design might reduce the tasks's sensitivity to measuring dispositional tendencies to engage cognitive offloading. In particular, the design introduces prediction errors, that could induce learning and interfere with natural tendencies to deploy reminder-setting behavior. These PEs comprise whether a given selected strategy will be or not be allowed to be engaged. We know individuals with compulsivity can learn even when instructed not to learn (e.g., Sharp, Dolan and Eldar, 2021, Psychological Medicine), and that more generally, they have trouble with structure knowledge (eg Seow et al; Fradkin et al), and thus might be sensitive to these PEs. Thus, a dispositional tendency to set reminders might be differentially impacted for those with compulsivity after an NPE, where they want to set a reminder, but aren't allowed to. After such an NPE, they may avoid moreso the tendency to set reminders. Those with compulsivity likely have superstitious beliefs about how checking behaviors lead to a resolution of catastrophes, that might in part originate from inferring structure in the presence of noise or from purely irrelevant sources of information for a given decision problem.<br /> It would be good to know if such learning effects exist, if they're modulated by PE (you can imagine PEs are higher if you are more incentivized - e.g., 9 points as opposed to only 3 points - to use reminders, and you are told you cannot use them), and if this learning effect confounds the relationship between compulsivity and reminder-setting.

A more subtle point, I think this study can be more said to be an exploration than a deductive of test of a particular model -> hypothesis -> experiment. Typically, when we test a hypothesis, we contrast it with competing models. Here, the tests were two-sided because multiple models, with mutually exclusive predictions (over-use or under-use of reminders) were tested. Moreover, it's unclear exactly how to make sense of what is called the direct mechanism, which is supported by the partial (as opposed to complete) mediation.

Author response:

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

Reviewer #1:

(1) You claim transdiagnostic phenotypes are temporally stable -- since they're relatively new constructs, do we know how stable? In what order?  

This is an important question. We have added two recent references to support this claim on page 1 and cite these studies in the references on pages 25 and 28:

“Using factor analysis, temporally stable (see Fox et al., 2023a; Sookud, Martin, Gillan, & Wise, 2024), transdiagnostic phenotypes can be extracted from extensive symptom datasets (Wise, Robinson, & Gillan, 2023).”

Fox, C. A., McDonogh, A., Donegan, K. R., Teckentrup, V., Crossen, R. J., Hanlon, A. K., … Gillan, C. M. (2024). Reliable, rapid, and remote measurement of metacognitive bias. Scientific Reports, 14(1), 14941. https://doi.org/10.1038/s41598-024-64900-0

Sookud, S., Martin, I., Gillan, C., & Wise, T. (2024, September 5). Impaired goal-directed planning in transdiagnostic compulsivity is explained by uncertainty about learned task structure. https://doi.org/10.31234/osf.io/zp6vk

More specifically, Sookud and colleagues found the intraclass correlation coefficient (ICC) for both factors to be high after a 3- or 12 month period (ICC_{AD_3} = 0.87; ICC_{AD_12} = 0.87; ICC_{CIT_3} = 0.81; ICC_{CIT_3}= 0.76; see Tables S41 and S50 in Sookud et al., 2024).

(2) On hypotheses of the study: 

I didn't understand the logic behind the hypothesis relating TDx Compulsivity -> Metacognition > Reminder-setting

It seems that (a) Compulsivity relates to overconfidence which should predict less remindersetting

Compulsivity has an impaired link between metacognition and action, breaking the B->C link in the mediation described above in (a). What would this then imply about how Compulsivity is related to reminder-setting?

"In the context of our study, a Metacognitive Control Mechanism would be reflected in a disrupted relationship between confidence levels and their tendency to set reminders."  What exactly does this predict - a lack of a correlation between confidence and remindersetting, specifically in high-compulsive subjects?

Lastly, there could be a direct link between compulsivity and reminder-usage, independent of any metacognitive influence. We refer to this as the Direct Mechanism  Why though theoretically would this be the case? 

"We initially hypothesised to find support for the Metacognitive Control Mechanism and that highly compulsive individuals would offload more". 

The latter part here, "highly compulsive individuals would offload more" is I think the exact opposite prediction of the Metacognitive control mechanism hypothesis (compulsive individuals offload less). How could you possibly have tried to find support, then, for both? 

Is the hypothesis that compulsivity positively predicts reminder setting the "direct mechanism" - if so, please clarify that, and if not, it should be added as a distinct mechanism, and additionally, the direct mechanism should be specified. 

There's more delineation of specific hypotheses (8 with caveats) in Methods. 

"We furthermore also tested this hypothesis but predicted raw confidence (percentage of circles participants predicted they would remember; H6b and H8b respectively)," What is the reference of "this hypothesis" given that right before this sentence two hypotheses are mentioned?  To keep this all organized, it would be good to simply have a table with hypotheses listed clearly. 

We agree with the reviewer that there is room to improve the clarity of how our hypotheses are presented. The confusion likely arises from the fact that, since we first planned and preregistered our study, several new pieces of work have emerged, which might have led us to question some of our initial hypotheses. We have taken great care to present the hypotheses as they were preregistered, while also considering the current state of the literature and organizing them in a logical flow to make them more digestible for the reader. We have clarified this point on page 4:

“Back when we preregistered our hypotheses only a limited number of studies about confidence and transdiagnostic CIT were available. This resulted in us hypothesising to find support for the Metacognitive Control Mechanism and that highly compulsive individuals would offload more due to an increased need for checkpoints.”

The biggest improvement we believe comes from our new Table 1, which we have included in the Methods section in response to the reviewer’s suggestion (pp. 21-22):

“We preregistered 8 hypotheses (see Table 1), half of which were sanity checks (H1-H4) aimed to establish whether our task would generally lead to the same patterns as previous studies using a similar task (as reviewed in Gilbert et al., 2023).”

We furthermore foreshadowed more explicitly how we would test the Metacognitive Control Mechanism in the Introduction section on page 4, as requested by the reviewer:

“In the context of our study, a Metacognitive Control Mechanism would be reflected in a disrupted relationship between confidence levels and their tendency to set reminders (i.e., the interaction between the bias to be over- or underconfident and transdiagnostic CIT in a regression model predicting a bias to set reminders).”

To avoid any confusion regarding the term ‘direct’ in the ‘Direct Mechanism’, we now explicitly clarify on page 4 that it refers to any non-metacognitive influences. Additionally, we had already emphasized in the Discussion section the need for future studies to specify these influences more directly.

Page 4: “We refer to this as the Direct Mechanism and it constitutes any possible influences that affect reminder setting in highly-compulsive CIT participants outside of metacognitive mechanisms, such as perfectionism and the wish to control the task without external aids.”

The reviewer was correct in pointing out that, in the Methods section, we incorrectly referred to ‘this hypothesis’ when we actually meant both of the previously mentioned hypotheses. We have corrected this on page 23:

“We furthermore also tested these hypotheses but predicted raw confidence (percentage of circles participants predicted they would remember; H6b and H8b respectively), as well as extending the main model with the scores from the cognitive ability test (ICAR5) as an additional covariate (H6c and H8c respectively).”

Finally, upon revisiting our Results section, we noticed that we had not made it sufficiently clear that hypothesis H6a was preregistered as non-directional. We have now clarified this on page 9:

“We predicted that the metacognitive bias would correlate negatively with AD (Hypothesis 8a; more anxious-depressed individuals tend to be underconfident). For CIT, we preregistered a non-directional, significant link with metacognitive bias (Hypothesis H6a). We found support for both hypotheses, both for AD, β = -0.22, SE = 0.04, t = -5.00, p < 0.001, as well as CIT, β = 0.15, SE = 0.05, t = 3.30, p = 0.001, controlling for age, gender, and educational attainment (Figure 3; see also Table S1). Note that for CIT this effect was positive, more compulsive individuals tend to be overconfident.”

(3) You say special circles are red, blue, or pink. Then, in the figure, the colors are cyan, orange, and magenta. These should be homogenized. 

Apologies, this was not clear on our screens. We have corrected this now but used the labels “blue”, “orange” and “magenta” as our shade of blue is much darker than cyan:

Page 16: “These circles flashed in a colour (blue, orange, or magenta) when they first appear on screen before fading to yellow.”

(4) The task is not clearly described with respect to forced choice. From my understanding, "forced choice" was implicitly delivered by a "computer choosing for them". You should indicate in the graphic that this is what forced choice means in the graphic and description more clearly. 

This is an excellent point. On pages 17 and 18 we now include a slightly changed Figure 6, which includes improved table row names and cell shading to indicate the choice people gave. Hopefully this clarifies what “forced choice” means.

(5) If I have point (4) right, then a potential issue arises in your design. Namely, if a participant has a bias to use or not use reminders, they will experience more or less prediction errors during their forced choice. This kind of prediction error could introduce different mood impacts on subsequent performance, altering their accuracy. This will have an asymmetric effect on the different forced phases (ie forced reminders or not). For this reason, I think it would be worthwhile to run a version of the experiment, if feasible, where you simply remove choice prior to revealing the condition. For example, have a block of choices where people can "see how well you do with reminders" -- this removes expectation and PE effects. 

[See also this point from the weaknesses listed in the public comments:]

Although I think this design and study are very helpful for the field, I felt that a feature of the design might reduce the tasks's sensitivity to measuring dispositional tendencies to engage cognitive offloading. In particular, the design introduces prediction errors, that could induce learning and interfere with natural tendencies to deploy reminder-setting behavior. These PEs comprise whether a given selected strategy will be or not be allowed to be engaged. We know individuals with compulsivity can learn even when instructed not to learn (e.g., Sharp, Dolan, and Eldar, 2021, Psychological Medicine), and that more generally, they have trouble with structure knowledge (eg Seow et al; Fradkin et al), and thus might be sensitive to these PEs. Thus, a dispositional tendency to set reminders might be differentially impacted for those with compulsivity after an NPE, where they want to set a reminder, but aren't allowed to. After such an NPE, they may avoid more so the tendency to set reminders. Those with compulsivity likely have superstitious beliefs about how checking behaviors leads to a resolution of catastrophes, which might in part originate from inferring structure in the presence of noise or from purely irrelevant sources of information for a given decision problem. 

It would be good to know if such learning effects exist if they're modulated by PE (you can imagine PEs are higher if you are more incentivized - e.g., 9 points as opposed to only 3 points - to use reminders, and you are told you cannot use them), and if this learning effect confounds the relationship between compulsivity and reminder-setting.

We would like to thank the reviewer for providing this interesting perspective on our task. If we understand correctly, the situation most at risk for such effects occurs when participants choose to use a reminder. Not receiving a reminder in the following trial can be seen as a negative prediction error (PE), whereas receiving one would represent the control condition (zero PE). Therefore, we focused on these two conditions in our analysis.

We indeed found that participants had a slightly higher tendency to choose reminders again after trials where they successfully requested them compared to after trials where they were not allowed reminders (difference = 4.4%). This effect was statistically significant, t(465) = 2.3, p = 0.024. However, it is important to note that other studies from our lab have reported a general, non-specific response ‘stickiness,’ where participants often simply repeat the same strategy in the next trial (Scarampi & Gilbert, 2020), which could have contributed to this pattern.

When we used CIT to predict this effect in a simple linear regression model, we did not find a significant effect (β = -0.05, SE = 0.05, t = -1.13, p = 0.26).

To further investigate this and potentially uncover an effect masked by the influence of the points participants could win in a given trial, we re-ran the model using a logistic mixed-effects regression model. This model predicted the upcoming trial’s choice (reminder or no reminder) from the presence of a negative prediction error in the current trial (dummy variable), the ztransformed number of points on offer, and the z-transformed CIT score (between-subject covariate), as well as the interaction of CIT and negative PE. In this model, we replicated the previous ‘stickiness’ effect, with a negative influence of a negative PE on the upcoming choice, β = -0.24, SE = 0.07, z = -3.44, p < 0.001. In other words, when a negative PE was encountered in the current trial, participants were less likely to choose reminders in the next trial. Additionally, there was a significant negative influence of points offered on the upcoming choice, β = -0.28, SE = 0.03, z = -8.82, p < 0.001. While this might seem counterintuitive, it could be due to a contrast effect: after being offered high rewards with reminders, participants might be deterred from using the reminder strategy in consecutive trials where lower rewards are likely to be offered, simply due to the bounded reward scale. CIT showed a small negative effect on upcoming reminder choice, β = -0.06, SE = 0.04, z = -1.69, p = 0.09, indicating that participants scoring higher on the CIT factor tended to be less likely to choose reminders, thus replicating one of the central findings of our study. It is unclear why this effect was not statistically significant, but this is likely due to the limited data on which the model was based (see below). Finally, and most importantly, the interaction between the current trial’s condition (negative PE or zero PE) and CIT was not significant, contrary to the reviewer’s hypothesis, β = 0.04, SE = 0.07, z = 0.57, p = 0.57.

It should also be noted that this exploratory analysis is based on a limited number of data points: on average, participants had 2.5 trials (min = 0; max = 4) with a negative PE and 6.7 trials (min = 0; max = 12) with zero PE. There were more zero PE trials simply because to maximise the number of trials included in this analysis, each participant’s 8 choice-only trials were included and on those trials the participant always got what they requested (the trial then ended prematurely). Due to the fact that not all cells in the analysed design were filled, only 466 out of 600 participants could be included in the analysis. This may have caused the fit of the mixed model to be singular.

In summary, given that these results are based on a limited number of data points, some models did not fit without issues, and no evidence was found to support the hypotheses, we suggest not including this exploratory analysis in the manuscript. However, if we have misunderstood the reviewer and should conduct a different analysis, we are happy to reconsider.

Unfortunately, conducting an additional study without the forced-choice element is not feasible, as this would create imbalances in trial numbers for the design. The advantage of the current, condensed task is the result of several careful pilot studies that have optimized the task’s psychometric properties.

Scarampi, C., & Gilbert, S. J. (2020). The effect of recent reminder setting on subsequent strategy and performance in a prospective memory task. Memory, 28(5), 677–691. https://doi.org/10.1080/09658211.2020.1764974

(6) One can imagine that a process goes on in this task where a person must estimate their own efficacy in each condition. Thus, individuals with more forced-choice experience prior to choosing for themselves might have more informed choice. Presumably, this is handled by your large N and randomization, but could be worth looking into. 

We would like to thank the reviewer for pointing this out, as we had not previously considered this aspect of our task. However, we believe it is not the experience with forced trials per se, but rather the frequency with which participants experience both strategies (reminder vs. no reminder), that could influence their ability to make more informed choices. To address this, we calculated the proportion of reminder trials during the first half of the task (excluding choiceonly trials, where the reminder strategy was not actually experienced). We hypothesized that the absolute distance of this ‘informedness’ parameter should correlate positively with the absolute reminder bias at the end of the task, with participants who experienced both conditions equally by the midpoint of the task being less biased towards or away from reminders. However, this was not the case, r = 0.05, p = 0.21.

Given the lengthy and complex nature of our preregistered analysis, we prefer not to include this exploratory analysis in the manuscript.

(7) Is the Actual indifference calculated from all choices? I believe so, given they don't know only till after their choice whether it's forced or not, but good to make this clear. 

Indeed, we use all available choice data to calculate the AIP. We now make this clear in two places in the main text:

Page 5: “The ‘actual indifference point’ was the point at which they were actually indifferent, based on all of their decisions.”

Page 6: “Please note that all choices were used to calculate the AIP, as participants only found out whether or not they would use a reminder after the decision was made.”

(8) Related to 7, I believe this implies that the objective and actual indifference points are not entirely independent, given the latter contains the former. 

Yes, the OIP and AIP were indeed calculated in part from events that happened within the same trials. However, since these events are non-overlapping (e.g., the choice from trial 6 contributes to the AIP but the accuracy measured several seconds later from that trial contributes to the OIP) and since our design dictates whether or not reminders can be used on those trials in question (by randomly assigning them to the forced internal/forced external condition) this could not induce circularity.

(9) I thought perfectionism might be a trait that could explain findings and it was nice to see convergence in thinking once I reached the conclusion. Along these lines, I was thinking that perhaps perfectionism has a curvilinear relationship with compulsivity (this is an intuition I'm not sure if it's backed up empirically). If it's really perfectionism, do you see that, at the extreme end of compulsivity, there's more reminder-setting? Ie did you try to model this relationship using a nonlinear function? You might clues simply by visual inspection. 

It is interesting to note that the reviewer reached a similar interpretation of our results. We considered this question during our analysis and conducted an additional exploratory analysis to examine how CIT quantile relates to reminder bias (see Author response image 1). Each circle reflects a participant. As shown, no clear nonlinearities are evident, which challenges this interpretation. We believe that adding this to the already lengthy manuscript may not be necessary, but we are of course happy to reconsider if Reviewer 1 disagrees.

Author response image 1.

(10) [From the weaknesses listed in the public comments.] A more subtle point, I think this study can be more said to be an exploration than a deductive test of a particular model -> hypothesis > experiment. Typically, when we test a hypothesis, we contrast it with competing models. Here, the tests were two-sided because multiple models, with mutually exclusive predictions (over-use or under-use of reminders) were tested. Moreover, it's unclear exactly how to make sense of what is called the direct mechanism, which is supported by partial (as opposed to complete) mediation.

The reviewer’s observation is accurate; some aspects of our study did take on a more exploratory nature, despite having preregistered hypotheses. This was partly due to the novelty of our research questions. We appreciate this feedback and will use it to refine our approach in future studies, aiming for more deductive testing.

Reviewer #2:

(1) Regarding the lack of relationship between AD and reminder setting, this result is in line with a recent study by Mohr et al (2023:https://osf.io/preprints/psyarxiv/vc7ye) investigating relationships between the same transdiagnostic symptom dimensions, confidence bias and another confidence-related behaviour: information seeking. Despite showing trial-by-trial under-confidence on a perceptual decision task, participants high in AD did not seek information any more than low AD participants. Hence, the under-confidence in AD had no knock-on effect on downstream information-seeking behaviour. I think it is interesting that converging evidence from your study and the Moher et al (2023) study suggest that high AD participants do not use the opportunity to increase their confidence (i.e., through reminder setting or information seeking). This may be because they do not believe that doing so will be effective or because they lack the motivation (i.e., through anhedonia and/or apathy) to do so. 

This is indeed an interesting parallel and we would like to thank the reviewer for pointing out this recently published study, which we unfortunately have missed. We included it in the Discussion section, extending our sub-section on the missing downstream effects of the AD factor, as well as listing it in the references on page 27.

Page 14: “Our findings align with those reported in a recent study by Mohr, Ince, and Benwell (2024). The authors observed that while high-AD participants were underconfident in a perceptual task, this underconfidence did not lead to increased information-seeking behaviour. Future research should explore whether this is due to their pessimism regarding the effectiveness of confidence-modulated strategies (i.e., setting reminders or seeking information) or whether it stems from apathy. Another possibility is that the relevant downstream effects of anxiety were not measured in our study and instead may lie in reminder-checking behaviours.”

Mohr, G., Ince, R.A.A. & Benwell, C.S.Y. Information search under uncertainty across transdiagnostic psychopathology and healthy ageing. Transl Psychiatry 14, 353 (2024). https://doi.org/10.1038/s41398-024-03065-w

(2) Fox et al 2023 are cited twice at the same point in the second paragraph of the intro. Not sure if this is a typo or if these are two separate studies? 

Those are indeed two different studies and should have been formatted as such. We have corrected this mistake in the following places and furthermore also corrected one of the references as the study has recently been published:

P. 2 (top): “Previous research links transdiagnostic compulsivity to impairments in metacognition, defined as thinking about one’s own thoughts, encompassing a broad spectrum of self-reflective signals, such as feelings of confidence (e.g., Rouault, Seow, Gillan & Fleming, 2018; Seow & Gillan, 2020; Benwell, Mohr, Wallberg, Kouadio, & Ince, 2022; Fox et al., 2023a;

Fox et al., 2023b; Hoven, Luigjes, Denys, Rouault, van Holst, 2023a).”

P. 2 (bottom): “More specifically, individuals characterized by transdiagnostic compulsivity have been consistently found to exhibit overconfidence (Rouault, Seow, Gillan & Fleming, 2018; Seow & Gillan, 2020; Benwell, Mohr, Wallberg, Kouadio, & Ince, 2022; Fox et al., 2023a; Fox et al., 2023b; Hoven et al., 2023a).”

P. 4: “Prior evidence exists for overconfidence in compulsivity (Rouault et al., 2018; Seow & Gillan, 2020; Benwell et al., 2022; Fox et al., 2023a; Fox et al., 2023b; Hoven et al., 2023a), which would therefore result in fewer reminders.”

P. 23: “Though we did not preregister a direction for this effect, in the light of recent findings it has now become clear that compulsivity would most likely be linked to overconfidence (Rouault et al., 2018; Seow & Gillan, 2020; Benwell et al., 2022; Fox et al., 2023a; Fox et al., 2023b; Hoven et al., 2023a).”

P. 24: “Fox, C. A., Lee, C. T., Hanlon, A. K., Seow, T. X. F., Lynch, K., Harty, S., … Gillan, C. M. (2023a). An observational treatment study of metacognition in anxious-depression. ELife, 12, 1–17. https://doi.org/10.7554/eLife.87193”

P. 24: “Fox, C. A., McDonogh, A., Donegan, K. R., Teckentrup, V., Crossen, R. J., Hanlon, A. K., … Gillan, C. M. (2024). Reliable, rapid, and remote measurement of metacognitive bias. Scientific Reports, 14(1), 14941. https://doi.org/10.1038/s41598-024-64900-0”

(3) Typo in the Figure 1 caption: "The preregistered exclusion criteria for the for the accuracies with....".  

Thank you so much for pointing this out. We haved changed the sentence in the caption of Figure 1 to read “The preregistered exclusion criteria for the accuracies with or without reminder are indicated as horizontal dotted lines (10% and 70% respectively).”

Typo in the Figure 5 caption: "Standardised regression coefficients are given for each pat".

Thank you so much for pointing this out to us, we have corrected the typo and the sentence in the caption of Figure 5 now reads “Standardised regression coefficients are given for each path.”

[From the weaknesses listed in the public comments.] Participants only performed a single task so it remains unclear if the observed effects would generalise to reminder-setting in other cognitive domains.

We appreciate the reviewer’s concern regarding the use of a single cognitive task in our study, which is indeed a common limitation in many cognitive neuroscience studies. The cognitive factors underlying offloading decisions are still under active debate. Notably, a previous study found that intention fulfilment in an earlier version of our task correlates with real-world behaviour, lending validity to our paradigm by linking it to realistic outcomes (Gilbert, 2015). Additionally, recent unpublished work (Grinschgl, 2024) has shown a correlation between offloading across two lab tasks, though a null effect was reported in another study with a smaller sample size by the same team (Meyerhoff et al., 2021), likely due to insufficient power. In summary, we agree that future research should replicate these findings with alternative tasks to enhance robustness.

Gilbert, S. J. (2015). Strategic offloading of delayed intentions into the external environment. Quarterly Journal of Experimental Psychology, 68(5), 971–992. https://doi.org/10.1080/17470218.2014.972963

Grinschgl, S. (2024). Cognitive Offloading in the lab and in daily life. 2nd Cognitive Offloading Meeting. [Talk]

Meyerhoff, H. S., Grinschgl, S., Papenmeier, F., & Gilbert, S. J. (2021). Individual differences in cognitive offloading: a comparison of intention offloading, pattern copy, and short-term memory capacity. Cognitive Research: Principles and Implications, 6(1), 34. https://doi.org/10.1186/s41235-021-00298-x

(6) [From the weaknesses listed in the public comments.] The sample consisted of participants recruited from the general population. Future studies should investigate whether the effects observed extend to individuals with the highest levels of symptoms (including clinical samples). 

We agree that transdiagnostic research should ideally include clinical samples to determine, for instance, whether the subclinical variation commonly studied in transdiagnostic work differs qualitatively from clinical presentations. However, this approach poses challenges, as transdiagnostic studies typically require large sample sizes, and recruiting clinical participants can be more difficult. With advancements in online sampling platforms, such as Prolific, achieving better availability and targeting may make this more feasible in the future. We intend to monitor these developments closely and contribute to such studies whenever possible.

Work culture is always undergoing change. The qoute that I highlighted undermines this premise. As we read throughout chapter 1, we learn about the vast differences of I/O Psychology throughout history and in different parts of the globe. For instance, we can evaluate gender differences through 1985-2003. Although this time frame may seem small in the context of our planet's history, we can actually observe a huge shift in the amount of women who entered the field of I/O Psychology, which doubled! Or, perhaps we can observe how the Civil Rights Act of 1964 affected work culture. As this ended employment discrimination, we can think about how diversity brought about so many new and fresh ideas to various work spaces. I/O Psychology is not the ultimate answer to solve all problems, but we can use it as an aid in changing our perspective and approach in workplace challenges. Whether it’s addressing issues of equity, enhancing collaboration, or improving employee well-being, I/O Psychology helps us navigate the complexities of an evolving work culture.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Strengths:

Overall there are some very interesting results that make an important contribution to the field. Notably, the results seem to point to differential recruitment of the PL-DMS pathway in goal-tracking vs sign-tracking behaviors.

Thank you.

Weaknesses:

There is a lot of missing information and data that should be reported/presented to allow a complete understanding of the findings and what was done. The writing of the manuscript was mostly quite clear, however, there are some specific leaps in logic that require more elaboration, and the focus at the start and end on cholinergic neurons and Parkinson's disease are, at the moment, confusing and require more justification.

In the revised paper, we provide additional graphs and information in support of results, and we further clarify procedures and findings. Furthermore, we expanded the description of the proposed interpretational framework that suggests that the contrasts between the cortical-striatal processing of movement cues in sign- versus goal trackers are related to previously established contrasts between the capacity for the  cortical cholinergic detection of attention-demanding cues.

Reviewer #2 (Public review):

Strengths:

The power of the sign- and goal-tracking model to account for neurobiological and behavioral variability is critically important to the field's understanding of the heterogeneity of the brain in health and disease. The approach and methodology are sound in their contribution to this important effort.

The authors establish behavioral differences, measure a neurobiological correlate of relevance, and then manipulate that correlate in a broader circuitry and show a causal role in behavior that is consistent with neurobiological measurements and phenotypic differences.

Sophisticated analyses provide a compelling description of the authors' observations.

Thank you.

Weaknesses:

It is challenging to assess what is considered the "n" in each analysis (trial, session, rat, trace (averaged across a session or single trial)). Representative glutamate traces (n = 5 traces (out of hundreds of recorded traces)) are used to illustrate a central finding, while more conventional trial-averaged population activity traces are not presented or analyzed. The latter would provide much-needed support for the reported findings and conclusions. Digging deeper into the methods, results, and figure legends, provides some answers to the reader, but much can be done to clarify what each data point represents and, in particular, how each rat contributes to a reported finding (ie. single trial-averaged trace per session for multiple sessions, or dozens of single traces across multiple sessions).

Representative traces should in theory be consistent with population averages within phenotype, and if not, discussion of such inconsistencies would enrich the conclusions drawn from the study. In particular, population traces of the phasic cue response in GT may resemble the representative peak examples, while smaller irregular peaks of ST may be missed in a population average (averaged prolonged elevation) and could serve as a rationale for more sophisticated analyses of peak probability presented subsequently.

We have added two new Tables to clarify the number of rats per phenotype and sex used for each experiment described in the paper (Table 1), and the number of glutamate traces (range, median and total number) extracted for each analysis of performance-associated glutamate levels and the impact of CNO-mediated inhibition of fronto-striatal glutamate (Table 3).

As the timing of glutamate peaks varies between individual traces and subjects, relative to turn and stop cue onset or reward delivery, subject-and trial-averaged glutamate traces would “wash-out” the essential findings of phenotype- and task event-dependent patterns of glutamate peaks. In the detailed responses to the reviewers, we illustrate the results of an analysis of averaged traces to substantiate this view. Furthermore, as detailed in the section on statistical methods, and as mentioned by the reviewer under Strengths, we used advanced statistical methods to assure that data from individual animals contribute equally to the overall result, and to minimize the possibility that an inordinate number of trials obtained from just one or a couple of rats biased the overall analysis.

Reviewer #3 (Public review):

Strengths:

Overall these studies are interesting and are of general relevance to a number of research questions in neurology and psychiatry. The assessment of the intersection of individual differences in cue-related learning strategies with movement-related questions - in this case, cued turning behavior - is an interesting and understudied question. The link between this work and growing notions of corticostriatal control of action selection makes it timely.

Thank you.

Weaknesses:

The clarity of the manuscript could be improved in several places, including in the graphical visualization of data. It is sometimes difficult to interpret the glutamate results, as presented, in the context of specific behavior, for example.

We appreciate the reviewer’s concerns about the complexity of some of the graphics, particularly the results from the arguably innovative analysis illustrated in Figure 6. Figure 6 illustrates that the likelihood of a cued turn can be predicted based on single and combined glutamate peak characteristics. The revised legend for this figure provides additional information and examples to ease the readers’ access to this figure. In addition, as already mentioned above, we have added several graphs to further illustrate our findings.

(Recommendations for the authors)

Reviewer #1 (Recommendations for the authors):

(1) The differences in behavioral phenotype according to vendor (Figure 1c) are slightly concerning, could the authors please elaborate on why they believe this difference is? Are there any other differences in these stocks- i.e. weight, appearance, other types of behaviors?

Differences in PCA behavior across vendors or specific breeding colonies were documented previously and may reflect the impact of environmental, developmental and genetic factors (references added in the revised manuscript). We included animals from both vendors to increase phenotypic variability and due to animal procurement constraints during COVID-related restrictions.

(2) Possibly related to the above, the rats in Figure 1a and Figure 2 are different strains. Please clarify.

In the revised legend of Figure 2 we clarify that the rat shown in the photographs is a Long-Evans rat that was not part of the experiments described in this paper. This rat was used to generate these photos as the black-spotted fur provided better contrast against the white treadmill belt.

(3) Figure 3c, the pairwise comparison showing a significant increase from Day 1 to Day 3 is hard to understand unless this is a lasting change. Is this increase preserved at Day 4? Examination of either a linear trend across days or a simple comparison of either Day 1 & 2 against Day 3 & 4 or, minimally Day 1 against Day 4 would communicate this message. Otherwise, there doesn't seem to be much of a case for improvement across test sessions, which would also be fine in my view.

As the analysis of post-criterion performance also revealed an effect of DAY, we felt compelled to report and illustrate the results of pairwise comparisons in Fig. 3c. In agreement with the reviewer’s point, we did not further comment on this finding in the manuscript.

(4) Figure 4e. I find it extremely unlikely that every included electrode was located exactly at anterior 0.5mm. Please indicate the range - most anterior and most posterior of the included electrodes in the study.

The schematic section shown in Fig. 4e depicted that AP level of that section and collapsed all placements onto that level. As detailed in Methods, electrode placements needed to be within the following stereotaxic space: AP: -0.3 to 0.6 mm, ML: 2 to 2.5 mm, and DV: -4.2 to -5 mm (see Methods). To clarify this issue, the text in Results and the legend was modified and the 0.5 mm label was removed from Fig. 4e.

(5) The paper generally is quite data light and there are a lot of extra results reported that aren't shown in the figures. There are 17 instances of the phrase "not shown", some are certainly justified, but a lot of results are missing…

We followed the reviewer’s suggestion and added several graphs. The revised Figure 5 includes the new graph 5d that shows the number of glutamate traces with just 1, 2 or 3 peaks occurring during cue presentation period. Likewise, the revised Figure 7 includes the new graph 7h that shows the number of glutamate traces with just 1, 2 or 3 peaks following the administration of CNO or its vehicle. In both cases, we also revised the analysis of peak number data, by counting the number of cases (or traces) with just 1, 2 or 3 peaks and using Chi-squared tests to determine the impact of phenotype and, in the latter case, of CNO. In addition, the revised Figure 7 now includes a graph showing the main effects of phenotype and CNO in reward delivery-locked glutamate maximum peak concentrations (Fig. 7k). In revising these sections, we also removed the prior statement about glutamate current rise times as this isolated observation had no impact on subsequent analyses or the discussion.

Concerning the reviewer’s point 5d (DMS eGFP transfection correlations Figure 8), the manuscript clarifies that the absence of such a correlation was expected given that eGFP expression in the DMS does not accurately reproduce the prelimbic-DMS projection space that was inhibited by CNO. In contrast, the correlations between the efficacy of CNO and DREADD expression measures in prelimbic cortex were significant and are graphed (Figs. 8g and 8j).

(6) Please clarify the exact number of animals in each experiment. The caption of Figure 3 seems to suggest there are 29 GTs and 22 STs in the initial experiment, but the caption of Figure 5b seems to suggest there are N=30 total rats being analyzed (leaving 21 un-accounted for), or is this just the number of GTs (meaning there is one extra)?

We have added Table 1 to clarify the number of animals used across different experiments and stages. Additionally, we have included a new Table 3 that identifies, for each graph showing results from the analyses of glutamate concentrations, the number of rats from which recordings were obtained and the number of traces per rat (range, median, and total).

(7) Relatedly, in Figures 5c-f and Figures 7g-i, the data seem to be analyzed by trial rather than subject-averaged, please clarify and what is the justification for this?

As detailed Experimental design and statistical analyses, we employed linear mixed-effects modeling to analyze the amperometric data that generated figures 5 and 7 to minimize the risk of bias due to an excessive number of trials obtained from specific rats. LMMs were chosen to analyze these repeated (non-independent) data to address issues that may be present with subject-averaged data. For clarity, throughout the results for these figures, the numerator in the F-ratio reflects the degrees of freedom from the fixed effects (phenotype/sex) and the denominator reflects the error term influenced by the number of subjects and the within-subject variance.

Concerning the illustration and analysis of trial- or subject-averaged glutamate traces please see reviewer 2, point 1 and the graph in that section. Within a response bin, such as the 2-s period following turn cues, glutamate peaks – as defined in Methods - occur at variable times relative to cue onset. Averaging traces over a population of rats or trials would “wash-out” the phenotype- and task event-dependent patterns of glutamate concentration peaks, yielding, for example, a single, nearly 2-s long plateau for cue-locked glutamate recordings from STs (see Figure 5b versus the graph shown in response to reviewer 2, point 1).

(8) Likewise on page 22, the number of animals from which these trials were taken should be stated "The characteristics of glutamate traces (maximum peak concentration, number of peaks, and time to peak) were extracted from 548 recordings of turn cue trials, 364 of which yielded a turn (GTs: 206, STs: 158) and 184 a miss (GTs: 112, STs: 72).".

The number of animals is now included in the text and listed in Table 3.

(9) The control group for Figure 7 given the mCherry fluorophore - given the known off-target effects of CNO, this is a very important control. Minimally, this data should be shown, but it is troubling that the ST group has n=2, I don't really understand how any sort of sensible stats can be conducted with a group this size, and obviously it's too small to find any significant differences if they were there.

As discussed on p. 14-15 in the manuscript under the section Clozapine N-Oxide, the conversion rate of CNO to clozapine suggests that approximately 50-100 times the dose of clozapine (compared to our 5.0 mg/kg CNO dosage) would be required to produce effects on rodent behavior (references on p. 14-15).

Regarding evidence from control rats expressing the empty construct, the revised manuscript clarifies that no effects of CNO on cued turns were found in 5 GTs expressing the empty control vector. Although CNO had no effects in STs expressing the DREADD, we also tested the effects of CNO in 2 STs expressing the empty control vector (individual turn rates following vehicle and CNO are reported for these 2 STs). Moreover, we extracted turn cue-locked glutamate traces (vehicle: 18 traces; 16 CNO traces) from an empty vector-expressing GT and found that administration of CNO neither reduced maximum glutamate peak concentrations nor the proportion of traces with just one peak. The absence of effects of CNO on cued turning performance and on turn-cue locked glutamate dynamics are consistent with prior studies showing no effects of 5.0 mg/kg CNO in rats not expressing the DREADD vector (references in manuscript).

(10) Figure 8b - the green circle indicated by 1 is definitely not the DMS, this is the DLS, and animals with virus placement in this region should be excluded.

The reviewer of course is correct and that exactly was the point of that illustration, as such a transfection space would have received the lowest possible rating (as indicated by the “1” in the green space). Fig. 8b was intended to illustrate expression efficacy ratings and does not indicate actual viral transfection spaces. Because the results described in the manuscript did not include data from a brain with a striatal transfection space as was illustrated in green in the original Fig. 8b, we removed that illustration of an off-target transfection space.  

(11) Figure 8j, the correlation specifically counts double-labeled PL hM4Di + eGFP neurons. Separating dual-labeled cells from all mCherry-labeled cells seems very strange given the nature of the viral approach. There seems to be an assumption that there are some neurons that express the mCherry-hM4Di that don't also have the AAV-Cre (eGFP). Obviously, if that were true this poses a huge problem for your viral approach and would mean that you're inhibiting a non-selective population of neurons. More likely, the AAV-Cre (eGFP) is present in all of your mCherry-hM4Di cells, just not at levels visible without GFP antibody amplification. Ideally, staining should be done to show that all cells with mCherry also have eGFP, but minimally this correlation should include all cells expressing mCherry with the assumption that they must also have the AAV-Cre.

As noted on page 15 in the Visualization and Quantification of eGFP/mCherry-Expressing Neurons section, eGFP expression in our viral approach was notably bright and did not necessitate signal enhancement. Furthermore, given the topographic organization of prelimbic-DMS projections on the on hand, and the variable transfection spaces in cortex and striatum on the other hand, the speculation that AAV-Cre may have been present in all mCherry cells is without basis. Second, there certainly are mCherry-positive cells that do not also express the retrogradely transported AAV-Cre, and that therefore were not affected by CNO. Third, the entire point of this dual vector strategy was to selectively inhibit prelimbic-striatal projections, and the strong correlation between double-labeled neuron numbers and cued turn scores substantiates the usefulness of this approach.

(12) Discussion, a bit more interpretation of the results would be good. Specifically - does the PL-DMS inhibition convert GTs to STs? There were several instances where the behavior and glutamate signals seemed to be pushed to look like STs but also a lot of missing data so it is hard to say. One would assume this kind of thing if, as I think is being said (please clarify), the ST phenotype is being driven by glutamatergic drive either locally or from sources other than PL cell bodies, presumably silencing the PL cell body inputs in GTs also leaves other glutamatergic inputs as the primary sources?

We agree with the reviewer that one could say, perhaps somewhat colloquially, that PL-DMS inhibition turns GTs to STs, in terms of turning performance and associated glutamate peak dynamics. The newly added data graphs are consistent with this notion. However, there are of course numerous other neurobiological characteristics which differ between GTs and STs and are revealed in the context of other behavioral or physiological functions.  In the Discussion, and as noted by the reviewer, we discuss alternative sources of glutamatergic control in STs and the functional implications of bottom-up mechanisms. In the revised manuscript, we have updated references and made minor revisions to improve this perspective.

(13) I found the abstract really detailed and very dense, it is pretty hard to understand in its current form for someone who hasn't yet read the paper. At this level, I would recommend more emphasis on what the results mean rather than listing the specific findings, given that the task is still quite opaque to the reader.

We revised the abstract, in part by deleting two rather dense but non-essential statements of results and by adding a more accessible conclusion statement.

(14) There are a lot of abbreviations: CTTT, PD, PCA, GT, ST, MEA, GO, LMM, EMMs, PL, DMS. Some of these are only mentioned a few times: MEA, LMM, and EMMs are all mentioned less than 5 times. To reduce mental load for the reader, you could spell these ones out, or include a table somewhere with all of the abbreviations.

We added a list of Abbreviations and Acronyms and eliminated abbreviations that were used infrequently.

(15) Generally, the logic that cortico-striatal connections contribute to GT vs ST seems easy to justify, however, the provided justification is missing a line of connection: "As such biases of GTs and STs were previously shown to be mediated in part via contrasting cholinergic capacities for the detection of cues (Paolone et al., 2013; Koshy Cherian et al., 2017; Pitchers et al., 2017a; Pitchers et al., 2017b), we hypothesized that contrasts in the cortico-striatal processing of movement cues contribute to the expression of these opponent biases." Please elaborate on why specifically cholinergic involvement suggests corticostriatal involvement. I think there are probably more direct reasons for the current hypothesis.

Done – see p. 4-5.

(16) Along the same line, paragraph 3 of the intro about Parkinson's disease and cholinergics seems slightly out of place. This is because the specific or hypothesized link between these things and corticostriatal glutamate has not been made clear. Consider streamlining the message specifically to corticostriatal projections in the context of the function you are investigating.

Done – see p. 4-5.

(17) Page 8, paragraph 2. There is a heading or preceding sentence missing from the start of this paragraph: "Contrary to the acclimation training phase, during which experimenters manually controlled the treadmill, this phase was controlled entirely by custom scripts using Med-PC software and interface (MedAssociates).".

Revised and clarified.

(18) Page 13 "We utilized a pathway-specific dual-vector chemogenetic strategy (e.g., Sherafat et al., 2020) to selectively inhibit the activity of fronto-cortical projections to the DMS". The Hart et al (2018) reference seems more appropriate being both the same pathway and viral combination approach.

Yes, thank you, we’ve updated the citation.

(19) Pages 20-21: "Maximum glutamate peak concentrations recorded during the cue period were significantly higher in GTs than in STs (phenotype: F(1,28.85)= 8.85, P=0.006, ηp 2=0.23; Fig. 5c). In contrast, maximum peak amplitudes locked to other task events all were significantly higher in STs." The wording here is misleading, both Figures 5c and 5d report glutamate peaks during the turn cue, the difference is what the animal does. So, it should be something like "Maximum glutamate peak concentrations recorded during the cue period were significantly higher in GTs than in STs when the animal correctly made a turn (stats) but this pattern reversed on missed trials when the animal failed to turn (stats)..." or something similar.

Yes, thank you. We have revised this section accordingly.  

(20) Same paragraph: "Contingency tables were used to compare phenotype and outcome-specific proportions and to compute the probability for turns in GTs relative to STs." What is an outcome-specific proportion?

This has been clarified.

.

(21) Page 22 typo: "GTs were only 0.74 times as likely as GTs to turn".

Fixed.

(22) The hypothesis for the DREADDs experiment isn't made clear enough. Page 23 "In contrast, in STs, more slowly rising, multiple glutamate release events, as well as the presence of relatively greater reward delivery-locked glutamate release, may have reflected the impact of intra-striatal circuitry and ascending, including dopaminergic, inputs on the excitability of glutamatergic terminals of corticostriatal projections" As far as I can understand, the claim seems to be that glutamate release might be locally modulated in the case of ST, on account of the profile of glutamate release- more slowly rising, multiple events, and reward-locked. Please clarify why these properties would preferentially suggest local modulation.

We have revised and expanded this section to clarify the basis for this hypothesis.

(23) The subheadings for the section related to Figure 7 "CNO disrupts..." "CNO attenuates..." presumably you mean fronto-striatal inhibition disrupts/attenuates. As it stands, it reads like the CNO per se is having these effects, off-target.

Fixed.

(24) The comparison of the results in the discussion against a "hypothetical" results section had the animals not been phenotyped behaviorally is unnecessary and overly speculative, given that 30-40% of rats don't fall into either of these two categories. I think the point here is to emphasize the importance of taking phenotype into account. This point can surely be made directly in its own sentence, probably somewhere towards the end of the discussion).

We have partly followed the reviewer’s advice and separated the discussion of the hypothetical results from the summary of main findings. However, we did not move this discussion toward the end of the Discussion section as we believe that it justifies the guiding focus of the discussion on the impact of phenotype.

(25) The discussion, like the introduction, talks a lot about cholinergic activity. As noted, this link is unclear - particularly how it links with the present results, please clarify or remove. Likewise high-frequency oscillations.

We have revised relevant sections in the Introduction (see above) and Discussion sections. However, given the considerable literature indicating contrasts between the cortical cholinergic-attentional capacities of GTs and STs, the interpretation of the current findings in that larger context is justified.

(26) Typo DSM in the discussion x 2.

Thanks, fixed.

Reviewer #2 (Recommendations for the authors):

(1) As mentioned in the Public Review, it is challenging to assess what is considered the "n" in each analysis, particularly for the glutamate signal analysis (trial, session, rat, trace (averaged across session or single trial)). Representative glutamate traces are used to illustrate a central finding, while more conventional trial-averaged population activity traces are not presented or analyzed. For example, n = 5 traces, out of hundreds of recorded traces, with each rat contributing 1-27 traces across multiple sessions suggests ~1-2% of the data are shown as time-resolved traces. Representative traces should in theory be consistent with population averages within phenotype, and if not, discussion of such inconsistencies would enrich the conclusions drawn from the study. In particular, population traces of the phasic cue response in GT may resemble the representative peak examples, while smaller irregular peaks of ST may be missed in a population average (averaged prolonged elevation in signal) and could serve as rationale for more sophisticated analyses of peak probability presented subsequently (and relevant to opening paragraph of discussion where hypothetical data rationale is presented).

We have added the new Table 1 to provide a complete account of the number of rats, per phenotype and sex, for each component of the experiments. In addition, the new Table 3 provides the range, median and total number of glutamate traces that were analyzed and formed the foundation of the individual data graphs depicting the results of glutamate concentration analyses.

We chose not to present trial- or subject-averaged traces, as glutamate peaks occur at variable times relative to the onset of turn and stop cues and reward delivery, and therefore averaging across a population of rats or trials would obscure phenotype- and task event-dependent patterns of glutamate peaks. The attached graph serves to illustrate this issue. The graph shows turn cue-locked glutamate concentrations (M, SD) from trials that yielded turns, averaged over all traces used for the analysis of the data shown in Fig. 5d (see also Table 3, top row). Because of the variability of peak times, trial- and subject-averaging of traces from STs yielded a nearly 2-s long elevated plateau of glutamate concentrations (red triangles), contrasting with the presence single and multiple peaks in STs as illustrated in Figs. 5b and 5e. Furthermore, averaging of traces from GTs obscured the presence of primarily single turn cue-locked peaks. Because of the relatively large variances of averaged data points, again reflecting the variability of peak times, analysis of glutamate levels during the cue period did not indicate an effect of phenotype (F(1,190)=1.65, P\=0.16). Together, subject- or trial-averaged traces would not convey the glutamate dynamics that form the essence of the amperometric findings obtained from our study. We recognize, as inferred by the reviewer, that smaller irregular peaks in STs may have been missed given the definition of a glutamate peak (see Methods). It is in part for that reason that we conducted a prospective analysis of the probability for turns given a combination of peak characteristics (maximum peak concentration and peak numbers; Fig. 6).

(2)To this latter point, the relationship between the likelihood to turn and the size of glutamate peak is focused on the GT phenotype, which limits understanding of how smaller multiple peaks relate to variables of interest in ST (missed turns, stops, reward). If it were possible to determine the likelihood for each phenotype, without a direct contrast of one phenotype relative to the other, this would be a more straightforward description of how signal frequency and amplitude relate to relevant behaviors in each group. Depending on the results, this could be done in addition to or instead of the current analysis in Figure 6.

We considered the reviewer’s suggestion but could not see how attempts to analyze the role of maximum glutamate concentrations and number of peaks within a single phenotype would provide any significant insights beyond the current description of results. Moreover, as stressed in the 2nd paragraph of the Discussion (see Reviewer 1, point 24), the removal of the phenotype comparison would nearly completely abolish the relationships between glutamate dynamics and behavior from the current data set.

Author response image 1.

(3) If Figure 6 is kept, a point made in the text is that GT is 1.002x more likely than ST to turn at a given magnitude of Glu signal. 1.002 x more likely is easily (perhaps mistakenly) interpreted as nearly identical likelihood. Looking closely at the data, perhaps what is meant is @ >4uM the difference between top-line labeled {b} and bottom-line labeled {d,e} is 1.002? If not, there may be a better way to describe the difference as 1x could be interpreted as the same/similar.

Concerning the potential for misinterpretation, the original manuscript stated (key phrase marked here in red font): Comparing the relative turn probabilities at maximum peak concentrations >4 µM, GTs were 1.002 times more likely (or nearly exactly twice as likely) as STs to turn if the number of cue-evoked glutamate peaks was limited to one (rhombi in Fig. 6a)  when compared to the presence of 2 or 3 peaks (triangles in Fig. 6a). However, we appreciate the reviewer’s concern about the complexity of this statement and, as it merely re-emphasized a result already described, it was deleted.

(4) For Figure 7e, the phenotype x day interaction is reported, but posthocs are looking within phenotype (GT) at treatment effects. Is there a phenotype x day x treatment, or simply phenotype x treatment (day collapsed) to justify within-group treatment posthocs?

We have revised the analysis and illustration of the data shown in Figs 7e and 7f, by averaging the test scores from the two tests, per animal, of the effects of vehicle and CNO, to be able to conduct a simpler 2-way analysis of the effects of phenotype and treatment.

(5) Ideally, viral control is included as a factor in this analysis as well. The separate analysis for viral controls was likely done due to low n, however negative findings from an ANOVA in which an n=2 (ST) should be interpreted with extreme caution. The authors already have treatment control (veh, CNO) and may consider dropping the viral controls completely due to the lack of power to perform appropriate analyses.

This issue has been clarified – see reviewer 1, point 9.

Minor:

(1) In the task description, it could be clearer how reward delivery relates to turns and stops. For example, does the turn cue indicate the rat will be rewarded at the port behind it? Does the stop cue indicate that the rat will be rewarded at the port in front of it? This makes logical sense, but the current text does not describe the task in this way, instead focusing on what is the correct action (seemingly but unlikely independent of reinforcement).

We have updated the task description in Methods and the legend of Figure 2 to indicate the location of reward delivery following turns and stops.

(2) For the peak analysis, what is the bin size for determining peaks? It is indicated that the value before and after the peak is >1 SD below the peak value, so it is helpful to know the temporal bin resolution for this definition.

As detailed on p 11-12 under Amperometry Data Processing and Analysis of Glutamate Peaks, we analyzed glutamate concentrations recorded at a frequency of 5 Hz (200 ms bins) throughout the 2-second-long presentation of turn and stop cues and for a 2-second period following reward delivery.

(3) Long Evans rats are pictured in Figure 2 (presumably contrast with a white background is better here), while SD rats are pictured in Figure 1. Perhaps stating why LE rats are pictured would help clear up any ambiguity about the strains used, as a quick look gives the impression two strains are used in two different tasks.

Yes, see reviewer 1, point 2.

(4) In Figure 7e, the ST and GT difference in turns/turn cue does not seem to replicate prior findings for tracking differences for this measure (Figure 3b). ST from the chemogenetic cohort seems to perform better than rats whose behavior was examined prior to glutamate sensor insertion. What accounts for this difference? Training and testing conditions/parameters?

The reviewer is correct. The absence of a significant difference between vehicle-treated GTs and vehicle-treated STs in Fig. 7e reflects a relatively lower turn rate in GTs than was seen in the analysis of baseline behavior (Fig. 3b; note the different ordinates of the two figures, needed to show the impact of CNO in Fig. 7e). Notably, the data in Fig. 7e are based on fewer rats (12 versus 29 GTs and 10 versus 22 STs; Table 1) and on rats which at this point had undergone additional surgeries to infuse the DREADD construct and implant electrode arrays. We can only speculate that these surgeries had greater detrimental effects in GTs, perhaps consistent with evidence suggesting that immune challenges trigger a relatively greater activation of their innate immune system (Carmen et al., 2023). We acknowledged this issue in the revised Results.

(5) The authors are encouraged to revise for grammar (are vs. is, sentence ending with a preposition, "not only" clause standing alone) and word choice (i.e. in introduction: insert, import, auditorily). Consider revising the opening sentence on page 5 for clarity.

We have revised the entire text to improve grammar and word choice.

(6) Do PD fallers refer to rats or humans? if the latter, this may be a somewhat stigmatizing word choice.

We have replaced such phrases using more neutral descriptions, such as referring to people with PD who frequently experience falls.

(7) Page 27 What does "non-instrumental" behavior mean?

We have re-phrased this statement without using this term.

(8) The opening paragraph of the discussion is focused on comparing reported results (with phenotype as a factor) to a hypothetical description of results (without phenotype as a factor) that were not presented in the results section. There is one reference to a correlation analysis on collapsed data, but otherwise, no reporting of data overall rats without phenotype as a factor. If this is a main focus, including these analyses in the results would be warranted. If this is only a minor point leading to discussion, authors could consider omitting the hypothetical comparison.

We have revised this section - see reviewer 1 point 24.

Reviewer #3 (Recommendations for the authors):

(1) These are really interesting studies. I think there are issues in data presentation/analysis that make it difficult to parse what exactly is happening in the glutamate signals, and when. Overall the paper is just a bit of a difficult read. A generally standard approach for showing neural recording data of many kinds, including, for example, subject-averaged traces, peri-event histograms, heatmaps, etc summarizing and quantifying the results - would be helpful. Beyond the examples in Figure 5, I would suggest including averaged traces of the glutamate signals and quantification of those traces.

We have addressed these issues in multiple ways, see the response to several points of reviewers 1 and 2, particularly reviewer 2, point 1.

(2) Figure 6 (and the description in the response letter) is also very non-intuitive. It's unclear how the examples shown relate to the reported significance indicators/labels/colors etc in the figure. I would suggest rethinking this figure overall, and if there is a more direct quantitative way to connect signal features with behavior. Again, drawing from standard visualization approaches for neural data could be one approach.

See also reviewer 2 points 1 and 3. Furthermore, we have revised the text in Results and the legend to improve the accessibility of Fig. 6.

(3) As far as I can tell, all of the glutamate sensor conclusions reflect analysis collapsed across 100s of trials. Do any of the patterns hold for a subjects-wise analysis? How variable are individual subjects?

We employed linear mixed-effect model analyses and added a random subject intercept to account for subject variability outside fixed effects (phenotype and treatment). The variance of the intercept ranged 0.01-1.71 SEM across outcome (cued turns/cued stops/misses). See also reviewer 1, point 7 and reviewer 2, point 1.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

We agree that numerous papers in the Statistical Learning literature discuss how different test measures can lead to different results and, in principle, using a different measure could have led to varying results in our study. In addition, we believe there are numerous additional factors relevant to this issue including the dichotomous vs. continuous nature of implicit vs. explicit learning and the complexity of the interactions between the (degree of) explicitness of the participants' knowledge and the applied test method that transcend a simple labeling of tests as implicit or explicit and that strongly constrains the type of variations the results of  different test would produce. Therefore, running the same experiments with different learning measures in future studies could provide additional interesting data with potentially different results.

However, the most important aspect of our reply concerning the reviewer's comment is that although quantitative differences between the learning rate of explicit and implicit learners are reported in our study, they are not of central importance to our interpretations. What is central are the different qualitative patterns of performance shown by the explicit and the implicit learners, i.e., the opposite directions of learning differences for “novel” and “same” structure pairs, which are seen in comparisons within the explicit group vs. within the implicit group and in the reported interaction. Following the reviewer's concern, any advantage an explicit participant might have in responding to 2AFC trials using “novel” structure pairs should also be present in the replies of 2AFC trials using the “same” structure pairs and this effect, at best, could modulate the overall magnitude of the across groups (Expl/Impl.) effect but not the relative magnitudes within one group. Therefore, we see no parsimonious reason to believe that any additional interaction between the explicitness level of participants and the chosen test type would impede our results and their interpretation.

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

We agree that this is a shortcoming of the current design, and obtaining the information about participants’ learning immediately after Phase 1 would have been preferred. However, we made this choice deliberately as the disadvantage of assessing the level of learning at the end of the experiment is far less damaging than the alternative of exposing the participants to the exit survey question earlier and thereby letting them achieve explicitness or influence their mindset otherwise through contemplating the survey questions before Phase 2. Our Experiment 5 shows how realistic this danger of unwanted influence is: with a single sentence alluding to pairs in the instructions of Exp 5, we  could completely change participants' quantitative performance and qualitative response pattern. Unfortunately, there is no implicit assessment of explicitness we could use in our experimental setup. We also note that given the cumulative nature of statistical learning, we expect that the effect of using an exit survey for this assessment only shifts absolute magnitudes (i.e. the fraction of people who would fall into the explicit vs. implicit groups) but not aspects of the results that would influence our conclusions.

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

The sample sizes of the explicit participants in our experiments are, indeed, much smaller than those of the implicit participants due to the process of how we obtain the members of the two groups. However, these sample sizes of the explicit groups are not small at all compared to typical experiments reported in Visual Statistical Learning studies, rather they tend to be average to large sizes. It is the sizes of the implicit subgroups that are unusually high due to the aforementioned data collecting process. Moreover, the explicit subgroups have significantly larger effect sizes than the implicit subgroup, bolstering the achieved power that is also confirmed by the reported Bayes Factors that support the “effect” or the “no effect” conclusions in the various tests ranging in value from substantial to very strong.  Based on these statistical measures,  we think the sample sizes of the explicit participants in our studies are adequate.

As for the lack of experimental control, indeed, we could not fully randomize consolidation condition assignment. Instead, the assignment was a product of when the study was made available on the online platform Prolific. This method could, in theory, lead to an unobserved covariate, such as morningness, being unbalanced between conditions. We do not have any reasons to believe that such a condition would critically alter the effects reported in our study, but as it follows from the nature of unobserved variables, we obviously cannot state this with certainty. Therefore, we added an explicit discussion of these potential pitfalls in the revised version of the manuscript.

Reviewer #3 (Public Review):

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

These results are interesting and can bridge several open gaps between different areas of study in learning and memory. However, I feel that a few issues in the manuscript need addressing for the results to be completely convincing:

(1) The reported studies have a wonderful and complex design. The complexity is warranted, as it aims to address several questions at once, and the data is robust enough to support such an endeavor. However, this work would benefit from more statistical rigor. First, the authors base their results on multiple t-tests conducted on different variables in the data. Analysis of a complex design should begin with a large model incorporating all variables of interest. Only then, significant findings would warrant further follow-up investigation into simple effects (e.g., first find an interaction effect between group and novelty, and only then dive into what drives that interaction). Furthermore, regardless of the statistical strategy used, a correction for multiple comparisons is needed here. Otherwise, it is hard to be convinced that none of these effects are spurious. Last, there is considerable variation in sample size between experiments. As the authors have conducted a power analysis, it would be good to report that information per each experiment, so readers know what power to expect in each.

Answering the questions we were interested in required us to investigate two related but separate types of effects within our data: general above-chance performance in learning, and within- and across-group differences.

Above-chance performance: As typical in SL studies, we needed to assess whether learning happened at all and which types of items were learned. For this, a comparison to the chance level is crucial and, therefore, one-sample t-test is the statistical test of choice. Note that all our t-tests were subject to experiment-wise correction for multiple comparisons using the Holm-Bonferroni procedure, as reported in the Supplementary Materials.

Within- and across-group differences: To obtain our results regarding group and par-type differences and their interactions, we used mixed ANOVAs and appropriate post-hoc tests as the reviewer suggested. These results are reported in the method section.

Concerning power analysis, in the revised version of the manuscript we added analysis of achieved power for the statistical tests most critical to our arguments.

(2) Some methodological details in this manuscript I found murky, which makes it hard to interpret results. For example, the secondary results section of Exp1 (under Methods) states that phase 2 foils for one structure were made of items of the other structure. This is an important detail, as it may make testing in phase 2 easier, and tie learning of one structure to the other. As a result, the authors infer a "consistency effect", and only 8 test trials are said to be used in all subsequent analyses of all experiments. I found the details, interpretation, and decision in this paragraph to lack sufficient detail, justification, and visibility. I could not find either of these important design and analysis decisions reflected in the main text of the manuscript or in the design figure. I would also expect to see a report of results when using all the data as originally planned.

We thank the reviewer for pointing out these critical open questions our manuscript that need further clarification. The inferred “consistency effect” is based on patterns found in the data, which show an increase in negative correlation between test types during the test phase. As this is apparently an effect of the design of the test phase and not an effect of the training phase, which we were interested in, we decided to minimize this effect as far as possible by focusing on the early test trials. For the revised version of the manuscript, we revamped and expanded the discussion of how this issue was handled and also add a short comment in the main text, mentioning the use of only a subset of test trials and pointing the interested reader to the details.

Similarly, the matched sample analysis is a great addition, but details are missing. Most importantly, it was not clear to me why the same matching method should be used for all experiments instead of choosing the best matching subgroup (regardless of how it was arrived at), and why the nearest-neighbor method with replacement was chosen, as it is not evident from the numbers in Supplementary Table 1 that it was indeed the best-performing method overall. Such omissions hinder interpreting the work.

Since our approach provided four different balanced metrics (see Supp. Tables 1-4) for each matching method, it is not completely straightforward to make a principled decision across the methods. In addition, selecting the best method for each experiment separately carries the suspicion of cherry-picking the most suitable results for our purposes. For the revised version, we expanded on our description of the matching and decision process and added supplementary descriptive plots showing what our data looks like under each matching method for each experiment. These plots highlight that the matching techniques produce qualitatively roughly identical results and picking one of them over the other does not alter the conclusions of the test. The plots give the interested reader all the necessary information to assess the extent our design decisions influence our results.

(3) To me, the most surprising result in this work relates to the performance of implicit participants when phase 2 followed phase 1 almost immediately (Experiment 1 and Supplementary Experiment 1). These participants had a deficit in learning the same structure but a benefit in learning the novel one. The first part is easier to reconcile, as primacy effects have been reported in statistical learning literature, and so new learning in this second phase could be expected to be worse. However, a simultaneous benefit in learning pairs of a new structure ("structural novelty effect") is harder to explain, and I could not find a satisfactory explanation in the manuscript.

Although we might not have worded it clearly, we do not claim that our "structural novelty effect" comes from a “benefit” in learning pairs of the novel structure. Rather, we used the term “interference” and lack of this interference. In other words, we believe that one possible explanation is that there is no actual benefit for learning pairs of the novel structure but simply unhindered learning for pairs of the novel structure and simultaneous inference for learning pairs of the same structure. Stronger interference for the same compared to the novel structure items seems as a reasonable interpretation as similarity-based interference is well established in the general (not SL-specific) literature under the label of proactive interference.

After possible design and statistical confounds (my previous comments) are ruled out, a deeper treatment of this finding would be warranted, both empirically (e.g., do explicit participants collapse across Experiments 1 and Supplementary Experiment 1 show the same effect?) and theoretically (e.g., why would this phenomenon be unique only to implicit learning, and why would it dissipate after a long awake break?).

Across all experiments, the explicit participants showed the same pattern of results but no significant difference between pair types, probably due to insufficiency of the available  sample sizes. We already included in the main text the collapsed explicit results across Experiments 1-4 and Supplementary Experiment 1 (p. 16).  This analysis confirmed that, indeed, there was a significant generalization for explicit participants across the two learning phases. We could re-run the same analysis for only Experiment 1 and Supplementary Experiment 1, but due to the small sample of  N=12 in Suppl. Exp. 1, this test will be likely completely underpowered. Obtaining the sufficient sample size for this one test would require an excessive number (several hundreds) of new participants.

In terms of theoretical treatment, we already presented our interpretation of our results in the discussion section, which we expanded on in the revised manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) It would be very useful to add individual data points (and/or another depiction of the distribution) to the bar plots. If not in the main figures, as added figures in the supplement.

We added violin plots for all results in the Supplementary.

(2) It would be helpful to include in the supplement some examples of responses that led to the 'explicit' or 'implicit' classification. Specifically, what kind of response was considered to contain a partial recognition of the underlying structure vs. no recognition?

We added example responses used for classification in the Supplementary.

(3) It would be useful to show the results of Experiment 5 as well as the diagonal version as supplemental figures.

We added the requested figures in the Supplementary.

Typos: page 10: "in in the tests", page 15: "rerun"

Fixed.

Reviewer #2 (Recommendations For The Authors):

(1) My strongest reservation relates to the small sample size in the explicit group. The authors do report stats for all experiments together in one analysis and I think this is the only robust finding for this group. I would suggest removing any comparisons between this smaller group and the larger implicit group since they do not make a lot of sense due to the imbalance in sample size in my opinion. If they do want to report the explicit group individually for each experiment, they should at least test for differences between the experiments also for this group using ANOVA.

We do agree that the unbalanced nature of the sample sizes can be problematic for the between-group comparisons. The t-tests reported for between-group comparisons are in fact Welch’s t-test better suited for unequal sample sizes and variances. Previously, we failed to report that these t-tests were Welch’s t-test, which we fixed in the revised version.

In the Supplementary, we previously reported an ANOVA including all explicit participants from all experiments. This showed a significant main effect of Experiment and test type, but no significant interaction. We take this as evidence that although specific levels of learning vary by experimental condition, the overall pattern of learning (i.e. which pairs are learned better) are the same across all experiments.

(2) Moreover, the explicit group does not only differ in the explicitness of their memory but also regarding learning performance per se (as evidenced by performance differences for the first training). This important confound needs to be acknowledged and discussed more thoroughly!

We agree that this topic is important, this is why the subsection “The Type of Transfer Depends on Quality of Knowledge, Not Quantity of Knowledge” deals exclusively with this issue. See our reply to the next point.

(3) The resampling approach is somewhat interesting to solve the issue raised in 2. However, I doubt that the authors actually achieve what they are claiming. Since we have a 2-AFC task the possibility must be considered that participants who chose correctly in the implicit group did so by chance. This means that the assumption that the matched pairs actually have the same amount of memory for the first training period as the explicit group is likely false. Therefore, this analysis is still comparing apples and oranges.

We address this idea in detail in the supplementary materials pointing out first that the matched results showed the same pattern as the full results suggesting that Phase 1 and Phase 2 results are independent for this group, and by arguing that randomly selected subset of participants should not show a significant deviation from null performance in the Same vs. Novel performance in Phase 2.

(4) One important issue, when conducting online experiments is assuring random allocation of participants. How did the authors recruit participants to ensure they did not select participants for the different experiments that differed regarding their preference for wake vs. sleep retention intervals? If no care was taken in this regard, I would suggest reporting this and maybe briefly discussing it.

This shortcoming was now reported and addressed in the discussion section of the revised manuscript.

(5) I could not find any information about the exact questions that were asked about the task rules. Also, there was no information on how the answers were used to assign groups. Both should be added.

The exact questions were added to the revised Supplementary.

(6) I think that the literature on sleep and rule extraction is well-represented in the manuscript. However, I think also referring more thoroughly to the literature on how sleep leads to gist extraction, schemas, and insight would help understand the relevance of the present research.

We subsumed references to the mentioned areas of research under the labels of abstraction and generalization. In the revised section, we listed the appropriate labels along with the already used references to make the connection to a vast literature treating generalization in related but distinct ways more explicit.

(7) It is unclear to me why the items learned in the first learning phase interfere with those learned in the second learning phase (without sleep) and not vice versa. What is the author's explanation for this?

We added a paragraph on this to our revised discussion section. In short, there may also be retroactive interference. However, we would need yet another variation of the paradigm to properly measure it, and this was outside the scope of the current work.

(8) As far as I can tell the study lacks all of the usual control tasks that are used in the field of sleep and memory (especially subjective sleepiness and objective vigilance). In addition, this research has the circadian confound, and therefore additional controls would have been warranted, e.g., morningness-eveningness, retrieval capabilities. Also, performance immediately after training phase 1 was not tested, which would serve as an important control for circadian differences in initial learning of the rule.

The study uses a number of the control measures established in the sleep and memory literature, such as habitual sleep quality and sleep quality during the night of and the night before the experiment. However, there are, of course, more potentially interesting measures, such as the ones named by the reviewer.

Testing performance right after training phase 1 would have been very interesting indeed. However, due to the nature of statistical learning tasks, this would have completely confounded the implicitness of learning by presenting participants with segmented input; i.e. isolated pairs. Therefore, we opted for the lesser of two evils in our design decision.

(9) As far as I can tell, there is no effect of sleep on correctly identifying pairs from training phase 1. This would be expected and thus should be discussed.

As noted and referenced in the discussion section, the effect of sleep on statistical learning per se is a subject of controversy in the literature, where some studies apparently find effects, while others find no effect on statistical learning whatsoever.

(10) The manuscript should explicitly mention if the study was preregistered.

It was not.

Reviewer #3 (Recommendations For The Authors):

The topic of this project is close to my heart, and I commend the authors for conducting numerous variations of the experiment with large sample sizes. I have some suggestions I feel will make the paper stronger, and a few minor comments that caught my eye during reading:

(1) First and foremost, I found the paper's structure cumbersome. For instance, different aspects of Experiment 1 results are reported in (1) the main text, (2) under methods, and (3) in Supplementary. This makes reading unnecessarily difficult. This relates not only to the analysis results - the sample size is reported as 226 in the main text, 226+3 in Methods, and 226+3+19 in Supplementary. I strongly suggest removing all results from the Methods section and merging the supplementary results with the main results.

We overhauled the structure of the paper, moving much more information into the proper method section and out of the Supplementary.

(2) "Attention checks" and "response bias" appear first in Supplementary Experiment 1 but are explained only later under Experiment 1. The same thing for the experimental procedure. I therefore suggest placing Experiment 1 before Supplementary Experiment 1, but related to my previous comment - have one paragraph dedicated to Subject Exclusion of all experiments.

The new structure of the Method sections solves this.

(3) Figure 4 is mentioned but does not appear in the manuscript.

This has been fixed. The paragraph in question now references the correct supplementary figure.

(4) OSF project includes only data with no README file on how to understand the data. The work would also benefit from sharing the experimental and analysis codes.

A README file was added.

(5) This sentence is repeated in relation to four experiments: "Bayes Factors from Bayesian t-tests for implicit participants reported for experiments 1, 2, and 3 used an r-scale parameter of 0.5 instead of the default √2/2, reflecting that Experiment 1 found small effect sizes for this group". First, it is missing an explanation of what the r-scale means. Second, it sounds as if this was a product of the procedure, but in fact it was a decision by the researcher if I am correct. If so, it is missing a description of how and why this choice was made.

This was indeed a decision by the researchers, in line with a Baysian logic of evidence accumulation. We made the explanation in the paper clearer.

(6) Did I understand correctly that each pair was tested 4 times? Was it against the same foil? Did you make sure not to repeat the same pair in back-to-back trials? These details, in addition to what I noted in the public review, are needed.

Each pair was tested 4 times. Each time against a different foil pair. Details have been added to the Method section.

(7) Also in relation to my public review, I could not understand why the sample size was overshot by so much in Experiment 1 (229 instead of 198.15)?

The calculated sample size of 198.15 was for the implicit subgroup alone, while 229 included explicit and implicit participants.

(8) The correlation between phase 1 and phase 2 is only tested in explicit participants. Why is that? A test in implicit participants is needed for completeness.

Correlations for implicit participants have been added.

(9) There is known asymmetry between the horizontal and vertical plains in our visual system (with preference for horizontal stimuli). I was missing a comparison between learning in the two structures, and a report of how many participants received either in Phase 1.

The allocation of participants to horizontal and vertical conditions was balanced. In the Method section we already report an ANOVA testing for a potential effect of orientation condition, which was not significant.

Minor/aesthetic comments:

(1) "In Phase 2, explicit participants performed above chance for learning pairs that shared their higher level orientation structure with that of pairs in Phase 1". This sounds as if there was a separate test following the two learning phases. Perhaps reword to "for phase 2 pairs".

Fixed

(2) "the two asleep-consolidation groups (Exp. 3 and 4)" - I think you mean Exp. 2 and 4.

Fixed.

(3) "acquiring explicitness in Experiment 5 as compared to 1" I think you mean Supplementary Experiment 1 as compared to 1.

Fixed

(4) "without such a redescription, the previously learned patterns in Phase 1 interfere with new ones in Phase 2, when redescription occurs..." The comma should be a dot.

Fixed

(5) In Experiment 4, did 168 or 169 participants survive exclusion? Both accounts exist, and so do reports of degrees of freedom that allow both 23 and 24 explicit participants.

Fixed.

(6) "Implicit learners also performed above chance.." in Experiment 2 is missing (n=XX).

Fixed.

Author response:

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

Public reviews:

We are grateful to the reviewers and the editorial team for their feedback and thorough revisions of our paper. We also appreciate their acknowledgement that this study represents a significant advancement in the field of reproductive neuroendocrinology and offers insights on the contribution of obesity vs melanocortin signaling in women’s fertility. In the revised version, we will provide a more detailed clarification of the data and methodology and adhere to the reviewers’ suggestions.

Please find below our answers to specific concerns in the public review:

Given the fact that mice lacking MC4R in Kiss1 neurons remained fertile despite some reproductive irregularities, the overall tone and some of the conclusions of the manuscript (e.g., from the abstract: "... Mc4r expressed in Kiss1 neurons is required for fertility in females") were overstated. Perhaps this can be described as a contributing pathway, but other mechanisms must also be involved in conveying metabolic information to the reproductive system.

We will tone down these statements throughout the manuscript to indicate that MC4R in Kiss1 neurons plays a role in the metabolic control of fertility (rather than “…is required for fertility”)

The mechanistic studies evaluating melanocortin signalling in Kiss1 neurons were all completed in ovariectomised animals (with and without exogenous hormones) that do not experience cyclical hormone changes. Such cyclical changes are fundamental to how these neurons function in vivo and may dynamically alter the way they respond to neuropeptides. Therefore, eliminating this variable makes interpretation difficult.

Mice lack true follicular and luteal phases and therefore it is impossible to separate estrogen-mediated changes from progesterone-mediated changes (e.g., in a proestrous female). Therefore, we use an ovariectomized female model in which we can generate a LH surge with an E2-replacement regimen [1]. This model enables us to focus on estrogen effects, exclude progesterone effects, and minimize variability. Inclusion of cycling females would make interpretation much more difficult.

(1) Bosch et al., 2013 Mol & Cell Endo; https://doi.org/10.1016/j.mce.2012.12.021

Use of the POMC-Cre to target ontogenetic inputs to Kiss1 neurons might have targeted a wider population of cells than intended.

POMC is transiently expressed during embryonic development in a portion of cells fated to be Kiss1 or NPY/AgRP neurons [1-2]. Therefore, this is a valid concern when crossing with a floxed mouse. However, use of AAVs in adult animals avoids this issue and leads to specific expression in POMC neurons [3]. This POMC-Cre mouse has been used extensively with AAVs to drive specific expression in POMC neurons by other laboratories [4-7]. Therefore, we are confident that our optogenetic studies have narrowly targeted POMC inputs.

(1) Padilla et al., 2010 Nat Med; https://doi.org/10.1038/nm.2126

(2) Lam et al., 2017 Mol Metab; https://doi.org/10.1016/j.molmet.2017.02.007

(3) Stincic et al., 2018 eNeuro; https://doi.org/10.1523/eneuro.0103-18.2018

(4) Fenselau et al., 2017 Nat Neuro; https://doi.org/10.1038/nn.4442

(5) Rau & Hentges, 2019 J Neuro; https://doi.org/10.1523/jneurosci.3193-18.2019

(6) Fortin et al., 2021 Nutrients; https://doi.org/10.3390/nu13051642

(7) Villa et al., 2024 J Neuro; https://doi.org/10.1523/jneurosci.0222-24.2024

Recommendations for Authors

We thank the reviewers and the editorial team for their comments and thorough revisions of our paper. We have now addressed their comments and edited the manuscript accordingly:

Reviewer #1 (Recommendations For The Authors):

L80 -This is an awkward sentence; it isn't an inverse agonist of the AgRP; this may read better just to say that the inverse agonist, AgRP.

Thank you for this comment. This has now been changed in the text (L80).

L86 - This text reads as if mice have an inherent obesity issue.

This has also now been addressed in the text (L86).

L131 - The numbers of digits past the decimal point should match for both mean and SEM.

This has also now been addressed throughout the text.

Figure 1D: Revise the bar graphs with distinct SEM bars, as these data are not generated within the same mice.

The graphs are now changed, and they include distinct SEM and individual data points.

Figure 2I-L - An n of 3 for controls is pretty minimal, though the clustering of data points is tight.

We thank the reviewer for this comment, and we emphasize that while we agree that an n=3 for controls is minimal, the mRNA level values of this group are close, therefore the clustering of the data points is tight. We are happy to provide the raw data value for these groups if the reviewer wishes to.

L159 - The role of reduced dynorphin mRNA is pretty speculative with regard to basal levels of LH, especially since no other indices of LH secretion were affected. It should also be recognized that mRNA levels do not always equate to activity.

We agree with the reviewer that our explanation of the role of the reduced dynorphin with regards to the elevated basal LH is speculative, however, we only report that the higher LH levels correlates with the lower expression of the Pdyn gene expression, which is in line with the well documented role of Dynorphin on inhibiting LH secretion. We also recognize that mRNA levels don’t necessarily reflect activity. We have now added this statement to the text (L159).

L164 - Given the ovary data, it seems that the increase seen in KO mice isn't quite sufficient, but is it known how much of a surge is necessary for ovulation in mice?

We agree with the reviewer’s comment that the LH surge in Kiss1MC4RKO group is not enough to consistently induce ovulation, which is supported by the decrease in the numbers of corpora lutea data (Figure 2, O).

According to literature, an LH surge in the female mice is estimated by a LH value >4 ng/ml (Bahougne et al., 2020). According to this rule, our data show that only two females out of six had LH surge in the KO group, while four females out of five had LH surge in the control group.  

L211 - According to the figure, LH pulses were not recovered and remained similar to KO levels. Looking at the LH secretory patterns presented, it seems like the pulse frequency data should be interpreted with some caution, given that some of the pulses identified are tenuous at best.

We agree that the LH pulses identified by our software (criteria described in the methods) are variable in shape (LH pulses are difficult to detect clearly in gonad intact females) and did not differ in number between groups; however, the reinsertion of Mc4r within Kiss1 neurons restored LH basal levels, amplitude and total secretory mass, which are clear indicatives of a significant improvement in the ability of these mice to release LH.

L218 - Is there a reason why the surge was not looked at in these groups?

Ovarian histology is the best indicator of ovulation. In these mice, corpora lutea were absent, indicating impaired ovulation, thus, we did not consider performing an LH surge protocol was necessary.

L244 - This would also fit with previous findings in sheep that not all Kiss neurons express MC receptors

We agree with this comment.

L329 - Given the rapidity of its actions, how would this membrane ER function during a normal surge?

Rapid estrogen signaling can act to ease transitions between states. Membrane delimited E2 actions can quickly attenuate or enhance coupling between receptors and signaling cascades. These effects will precede E2-driven changes in gene expression that produce more stable alterations in signaling. This combination of mechanisms will reduce any lag between rises in serum E2 and physiological effects. Considering the abbreviated mouse reproductive cycle, parallel mechanisms acting on different timescales are particularly important.

L365 - I'm a little confused as to how this particular work sheds light on a role for MC3R. Is the relative distribution of the two isoforms within Kiss neurons known?

In the present study, we report that hypothalamic Mc3r expression decreases leading up to the age of puberty onset (p30), in line with the profile of expression of Mc4r and a recent publication involving Mc3r in puberty onset (Lam et al., 2021), suggesting that both receptors may be involved in the control of reproductive function, potentially through the direct regulation of Kiss1 neurons as characterized in our present study.

L422 - While I understand the nature of this statement, the receptor may simply reflect the activity of what binds to it, i.e., AgRP vs. alpha-MSH, suggesting that maybe the prepubertal period is more AgRP-dominated.

We agree with this statement, and this needs to be further investigated.

L495 - Reinsertion of Mc4R in Kiss1 neurons

Thank you for this comment. This is now corrected in the text (L501).

L524 - Bilateral ovariectomy of 6-month

Thank you for this comment. This is now corrected in the text (L530).

L538 - Is it known what stage of the cycle these mice were in when samples were collected?

Yes, the samples were collected in diestrus. This is now mentioned in the text (L548)

L556 - Pulse amplitude is usually measured relative to the preceding nadir.

The method that we have been consistently using in our lab is the average of the 4 highest LH values in the samples collection period for each animal. We have found this to be consistent and representative of the overall amplitude (McCarthy et al., 2021; Talbi et al., 2021).

L594 - This is a little confusing - the whole MBH would contain the ARH, but only the ARH was collected from the KO mice. If the whole MBH, dynorphin and Tac3, and Tac3 are expressed outside of the ARC, making interpretation of changes specifically within the ARH is difficult.

Here (L592), we describe two different experiments, as mentioned by i) and ii).

For experiment 1 (i): MBH was used in the WT mice at ages P10, P15, P22 and P30 to investigate the expression of the melanocortin genes (Agrp, Pomc, Mc3r and Mc4r).

For experiment 2 (ii): In both KO and control groups, only the micro-dissected ARH was used to investigate genes expressions of Pdyn, Kiss1, Tac2, Tacr3.

Reviewer #2 (Recommendations For The Authors):

The validation experiments for the various manipulations are currently presented in the supplementary data. Still, in my opinion, these are critically important for interpreting the data, and it should be considered to present these more comprehensively in the main body of the manuscript. In Figure S1, it seems that the exposure of the two images is not the same, with a higher background in the control. Has this image been adjusted to highlight the staining, while the other has not? It looks like there remains a low level of expression still present in at least some of the KO cells - this may reflect difficulties using RNAscope (with its extreme amplification) to detect the absence of a signal, or it could also be that the knockout is incomplete. A percentage of cells still express MC4R. I think this should be acknowledged or discussed.

We thank the reviewer for the feedback. While we agree that the validation of the mouse model is critical, we would like to keep it in the supplemental data.

We also agree that the exposure looks different between the KO and WT controls, and we thank the reviewer for this comment. The quality of the photograph decreased when transferring to the manuscript. This has now been improved in the revised figure.

As for the MC4R expression in some of the KO cells, we believe that MC4R is expressed in non Kiss1 cells as shown in the merged figure. Therefore, we believe that the Knockout of Mc4r in Kiss1 neurons is complete in these mice.

The clear difference from the PVN's lack of effect is convincing and indicates that a specific knockout has been achieved. Is equivalent data also available for the AVPV population of cells that are examined later in the manuscript? Do those Kiss1 neurons also express the MC4R? The same question applies to the knock-in experiment: Was the expression of MC4R also driven in the AVPV population using this approach

Yes, Kiss1 neurons in the AVPV also express MC4R as indicated in this study, and thus Mc4r is removed/reinserted in the AVPV as well in this mouse model.

The quantitative RT-qPCR data on developmental changes in metabolic signaling molecules are really peripheral to the paper's main question. Relative to the validation experiments (as discussed above), I think these are less important data and could be placed into a supplementary figure. The discussion of these data becomes problematic, e.g., on line 359, the changes are described as "a low melanocortin tone..." but this seems problematic when referring to reduced expression of AgRP, an inverse agonist at the MC4R. If you are going to present these data, individual data points should be shown. Similarly, the question about whether this is a PCOS-like phenotype is perhaps worth asking. Still, the simple assessment of T and AMH could also be reported in a sentence without necessarily showing the data (or placing it in a supplementary figure). Better to focus on the key question - which is the role of MC4R signaling in Kiss1 neurons.

We understand this reviewer’s concerns, however, due to the impact of MC4R signaling (particularly in the context of AgRP) on puberty, we strongly believe that the reader will benefit from expression profile across ages so we will respectfully disagree and keep in the main figure.  

Per this reviewer’s comment, we have now added individual data points to Figure 1D.

We also agree with the reviewer that the T and AMH data are not in the main scope of the paper, but since we uncovered a PCOS-like phenotype in female mice with specific deletion of Mc4r from Kiss1 neurons, it is important to keep these data in the main figure to show that the phenotype does not fully resemble a PCOS model.

Having praised the experimental design, I think it is fair to acknowledge that the reproductive data from these experiments remain difficult to interpret. I understand that it is difficult to illustrate estrous cycles, but the "quantitative" data on percentages of time spent in any one stage are not as informative as seeing the actual individual patterns in Figure 2B. Were all of the animals consistently like the one illustrated, with persistent diestrus and only occasional evidence of ovulation?

We agree that Figure 2C may be difficult to interpret but it is the best way to capture the all the data points for each group.

All the 5 Kiss1MC4RKO females had persistent diestrus phases with only one or two estrus phases over 15 days (except for one female who had 4 estrous days), compared to control females who had 7 to 9 days of estrous, as shown in the graph (except for one female who had 5 days of estrus over 15 days period).

Given that LH pulses appear to be normal, does this, in fact, suggest an ovarian problem? Is that possible? Are MC4R and Kiss1 co-expressed in the ovary? Or do you think this suggests an ovulation problem, perhaps driven by the impaired LH surge?

This reviewer is correct in that our findings suggest a central defect in ovulation based on the deficit observed in the preovulatory LH surge. Thus, it is possible to have normal LH pulses, which are driven by one population of Kiss1 neurons (ARH) and the LH surge, driven by a distinct population of Kiss1 neurons (AVPV).

Similarly, the response to the "LH surge induction protocol" is impaired (why not look at endogenous LH surges?). It seems that ovulation should be an all-or-none phenomenon in that if the LH surge is sufficient to induce ovulation, then all available follicles would be ovulated. If it is not, then no follicles will be ovulated. Why fewer follicles are ovulated in the gene-targeted animals seems more likely to be due to impaired follicular development rather than a subthreshold LH surge. So, this again points back to the ovary. Or perhaps we need a more thorough assessment of the pattern of LH pulses throughout the cycles in these animals.

An LH surge induction protocol allows us to submit all female mice to the same conditions and expect a similar response, which is then optimal to compare with animals with an expected ovulation deficit, as it eliminates   external factors. We disagree in that ovulation is an all-or-none phenomenon because in mice numerous follicles mature at the same time and thus a decrease in the number of ovulated oocytes may be significant between groups even if the animals are not completely infertile.

Collectively, my assessment of these data is that there are effects on reproduction, but they are actually relatively subtle. There were abnormal cycles and impaired LH surge in response to exogenous estrogen. But the animals are not actually infertile, so can ovulate and express normal reproductive behavior. So while there is a role for MC4R signalling in Kiss1 neurons, it may be a contributing modulatory role rather than a major regulatory mechanism. I think the tone of the descriptions should reflect this. I like the way it is framed in some parts of the discussion ("reproductive impairments...mediated by MC4R in Kiss1 neurons and not by their obese phenotype"), but the overall significance of this is overstated in some places, such as the abstract and in other parts of the discussion ("this population is tightly controlled by melanocortins").

As mentioned in previous responses, ovulation in mice is not all-or nothing, so while the mice can reproduce, the disruption in the central mechanisms that control ovulation and irregular estrous cycles are a significant advancement in the field with strong translational potential to species where only one oocyte is usually ovulated, like in humans, where reproductive disorders in MC4R patients had been attributed to the obesity phenotype rather than to a central action of MC4R (as the reviewer captured in their comment). This is one of the main findings of this study.

The overstatement has been now addressed throughout the text.

For in vitro studies, all mice were ovariectomized and given estradiol "replacement." What was the rationale for this? Wouldn't this suppress the basal activity of these neurons? Then it appears that some of the animals were studied as ovariectomised (for an unspecified time but apparently ">7 days", without hormone replacement. The basal activity of these cells would be dramatically different. I think these artificial manipulations make these data quite difficult to interpret. How does this reflect the situation in a normal (or abnormal) estrous cycle? My understanding is that the brain slice approach already compromises the ability of this population of cells to function as a coordinated network (i.e., coordinated episodes of activity that are seen in vivo have not been observed in vitro in brain slices). Ovariectomizing and providing exogenous hormones also removes the additional regulatory elements of the cyclical changes in hormone inputs, so the cells may or may not behave like they would in vivo. Perhaps the authors could justify their choice of experimental model.

We have clarified that the mice were ovariectomized for 7-10 days. A group of 3 mice are OVXed at once and then used on subsequent days a week later. This delay is both for the recovery of the animal and to allow for “washout” of endogenous ovarian hormones. For optogenetic studies, we were not measuring basal activity. Rather, we prioritized the ability to detect a postsynaptic response. While E2 decreases the networked activity of Kiss1- ARH neurons, the Hcn channels, calcium channels, and Vglut2 expression are all increased. This leads to increased excitability and more glutamate release. Mice lack true follicular and luteal phases and therefore it is impossible to separate estrogen-mediated changes from progesterone-mediated changes (e.g., in a proestrous female). Therefore, we use an ovariectomized female model in which we can generate a LH surge with an E2-replacement regimen (Bosch et al., J Mol Cell Endocrinology 2013). This model enables us to focus on estrogen effects, exclude progesterone effects, and minimize variability. Finally, we have documented that Kiss1^ARH neurons retain the synchronization of their neuronal firing in the hypothalamic slice preparation (Qiu et al., eLife 2016).

Figure 4E shows neurons' staining after expressing a Cre-dependent channel rhodopsin vector into POMC-Cre mice. The number of labelled cells looks markedly larger than expected for adult POMC neurons. Was the specificity of this approach to neurons expressing POMC checked? I understand that the POMC-Cre mice have been criticised for ectopic expression of Cre during development in other populations of neurons in the arcuate nucleus that does not express POMC, such as the AgRP neurons (e.g., PMID: 22166984). Is it possible that this is not a problem in adult animals? Has that been validated in these animals? The description of the method suggests that it is acknowledged that some of the expression driven in these animals might be in AgRP neurons. Still, optogenetic activation of these cells will include all cells expressing Cre at the time of AAV administration.

POMC is transiently expressed during embryonic development in a portion of cells fated to be Kiss1 or NPY/AgRP neurons. Therefore, this is a valid concern when crossing with a floxed mouse. However, use of AAVs in adult animals avoids this issue and leads to specific expression in POMC neurons. This POMC-Cre mouse has been used extensively with AAVs to drive specific expression in POMC neurons by other laboratories (Padilla et al., Nat Med 2010; Lam et al., Mol Metab 2017; Stincic et al., eNeuro 2018 eNeuro; Fenselau et al., Nat Neuro 2017). We have previously shown that AAV-driven mCherry expression is limited to cells labeled with a beta-endorphin antibody (Stincic et al., 2018 eNeuro). Therefore, we are confident that our optogenetic studies have narrowly targeted POMC inputs.

Some additional explanation of the electrophysiology result may be required. For example, on Line 292, I'm confused by Fig 4M. Why is the response to 20Hz stimulation different in this cell (compared to the one in 4L) before administering naloxone? What proportion of cells showed this opposite response? On line 307: Is 5 cells sufficient for testing the POMC inputs onto AVPV and PeN Kiss1 neurons? How many slices/animals are included in collecting these 5 cells? The rapid action of STX illustrates the ability to modulate the response to MTII, but I am struggling to understand the implications of this in a physiological context. Suppose this response is desensitized by longer-term treatment with E2 (as indicated in the manuscript). Is it relevant to normal regulation during the cycle (particularly in the AVPV, where the key regulatory step seems to be the prolonged exposure to high estradiol as part of the preovulatory signals leading up to the LH surge)?

As stated in the text, E2 has been shown to increase POMC expression and beta-Endorphin immunostaining. We do not know the effects of E2 on aMSH expression and release. E2 also tends to attenuate the coupling between inhibitory postsynaptic metabotropic (Gi,o-coupled) receptors and signaling cascades. So, there is likely a combination of pre- and post-synaptic mechanisms contributing to these responses. However, the focus of the current studies was on the predominant melanocortin signaling and, as such, we chose to eliminate the influence of opioid signaling. We have added two more cells to this group, both of which were successfully rescued for a total of 5 of 6 cells (6 slices, 5 animals). Between the labeling of b-endorphin fibers and high rate of rescue, we do believe that this is sufficient evidence to support a direct POMC input to Kiss1^AVP/PeN neurons.

Line 52: "Here, we show that Mc4r expressed in Kiss1 neurons is required for fertility in females." The knockout animals remain fertile, so this conclusion needs to be re-worded.

Thank you for this comment. This has now been changed (L52).

Line 80: "The melanocortin 4 receptor (MC4R) binds α-melanocyte stimulating hormone (αMSH), an agonist product of the pro-opiomelanocortin (Pomc) gene, and the inverse agonist of the agouti-related peptide (AgRP) to regulate food intake and energy expenditure" Is this the correct wording? I think it should be stated that AgRP is an inverse agonist at the MC4R, not that αMSH is the inverse agonist of AgRP. Re-work this sentence.

Thank you for this comment. This has now been changed (L79-80).

Line 88: "... however, conflicting reports exist". Describe what these conflicting reports show. Many MC4 variants ("mutations") are expressed in humans, but few will fully inactivate signalling like the mouse knockout.

We thank the reviewer for this comment. By conflicting data, we refer to the studies that report no reproductive impairments in women with MC4R mutations. Either because the metabolic impairments (obesity, hyperphagia, hyperinsulinemia, hyperleptinemia, etc) are so strong that the focus is skewed to these issues, without a full reproductive assessment in these women, or simply because the reviewer mentioned, not all MC4R mutations fully inactivate its signaling in humans - as opposed to mouse models where reproductive disruption has been described previously in full body MC4RKOs.

Line 91: "...that largely affects females". Is this a genuine sex difference, or are reproductive deficits simply more overt in female rodents? I think the Coss paper (reference 19 in the manuscript) showed a greater effect of diet-induced obesity in males than in females.

We believe that sex differences exist with regards to the role of MC4R in the regulation of fertility, as we show that most of this effect is mediated by MC4R signaling in Kiss1 AVPV neurons, a neuronal population that is specific to the female brain.

As far as we can tell, the Coss paper (Villa et al., 2024) has only tested males but not females. Moreover, they investigated the effect of diet induced obesity in mice on their fertility (specifically LH secretion), while in this study we are specifically looking at the deletion of MC4R from Kiss1 neurons, and these mice were not obese (Figure 2A). While both these conditions induce impaired fertility, the mechanisms and signaling pathways are different (our mice lack MC4R signaling while the obese mice have a decrease in MC4R expression but the signaling is still functional).

Line 392: also Hessler et al. PMID: 32337804.

This reference is now added to the text (Line 393).

Line 433. The discussion of how advanced puberty onset (seen in the Kiss1-specific KO animals) might be caused by MC4R signalling in AVPV Kiss1 neurons, which are sexually dimorphic, which might explain sex differences in puberty timing in mammals seems extremely speculative and based on limited data. More targeted experiments would be needed to address this, and I think this speculation should be removed here.

This speculation has now been removed from the text.

Line 438: "Furthermore, our findings suggest that metabolic cues, through the regulation of the melanocortin output onto Kiss1AVPV/PeN neurons, are essential for the timing and magnitude of the GnRH/LH surge." Again, I think this is overstating the present data, which has only looked at an artificial hormone administration regime. The animals are fertile and, thus, must be able to mount a sufficient LH surge. The major effect, in fact, seems to be on their cycle, perhaps leading to impaired follicular development. Please acknowledge that this will be one of the multiple pathways by which metabolic information is fed into the HPG axis.

In addition to the effect on their cycles as mentioned by the reviewer, the Kiss1MC4RKO females also display impaired fertility (Figure 2, S-T) and fewer corpora lutea which is in line with the impaired mounting of LH surge (Figure 2, M). Even if the LH surge is induced by the hormone administration protocol, it only reflects the natural ability of the HPG axis to mount the surge, as this regimen is only there to mimic the endogenous hormonal changes leading to LH surge and therefore ovulation, in a controlled manner. Nonetheless, we agree with this reviewer that this is not the sole mechanism by which metabolism regulates reproductive function and this has been emphasized in the paper. (line 443)

Reviewer #3 (Recommendations For The Authors):

The decreased melanocortin tone drives puberty onset (Figure 1D), and this is correlative. The transgenic animals' hypothalamic expression of Agrp, Pomc, Mc4r, and Mc3r can be measured to strengthen the claim. Hprt expression should be demonstrated, as this housekeeping gene was used as a common denominator.

We thank the reviewer for this comment. While we think that indeed, measuring Agrp, Pomc, Mc4r, and Mc3r gene expressions in the transgenic mice will strengthen our claim and give more insights into the melanocortins tone during pubertal maturation, this is unfortunately not feasible as it will involve generating a lot of mice (at least n=40 pups for an n=5/group, KO and control littermates, females only -which will require setting up lots of breeding pairs-) during different ages throughout puberty.

As for the gene expression of Hprt, because we have 6 mice per age, 4 ages total, every gene (Agrp, Pomc, Mc4r, Mc3r) was run in a separate plate with Hprt as its own housekeeping gene. Samples were run in duplicates for each Hprt and melanocortin genes in a 96 well = 48 wells for Hprt and 48 wells for each of the melanocortin genes. Therefore, it won’t be possible to represent one Hprt expression for all the four genes, however every gene was normalized to the Hprt gene expression that was ran in the same plate).

In Figures 4 and 5, dot plots can be used (as opposed to the bar graphs) to better reflect the individual data points.

Figures 4 and 5 have been revised to include individual data points.

The electrophysiology experiment requires more details in the method section. In addition to the publication cited, a brief recap of the methodology used in this paper, such as the focal application of MTII (Figure 4B), is also needed.

We have added more details to the Methods.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The authors observed a decline in autophagy and proteasome activity in the context of Milton knockdown. Through proteomic analysis, they identified an increase in the protein levels of eIF2β, subsequently pinpointing a novel interaction within eIF subunits where eIF2β contributes to the reduction of eIF2α phosphorylation levels. Furthermore, they demonstrated that overexpression of eIF2β suppresses autophagy and leads to diminished motor function. It was also shown that in a heterozygous mutant background of eIF2β, Milton knockdown could be rescued. This work represents a novel and significant contribution to the field, revealing for the first time that the loss of mitochondria from axons can lead to impaired autophagy function via eIF2β, potentially influencing the acceleration of aging. To further support the authors' claims, several improvements are necessary, particularly in the methods of quantification and the points that should be demonstrated quantitatively. It is crucial to investigate the correlation between aging and the proteins eIF2β and eIF2α.

Thank you so much for your review and comments. We included analyses of protein levels of eIF2α, eIF2β, and eIF2γ at 7 days and 21 days (Figure 4D). The manuscript was revised as below;

Lines 242-245 ‘As for the other subunits of eIF2 complex, proteome analysis did not detect a significant difference in the protein levels of eIF2α and eIF2γ between milton knockdown and control flies at 7 and 21 days (Figure 4D).’

Reviewer #2 (Public Review):

In the manuscript, the authors aimed to elucidate the molecular mechanism that explains neurodegeneration caused by the depletion of axonal mitochondria. In Drosophila, starting with siRNA depletion of Milton and Miro, the authors attempted to demonstrate that the depletion of axonal mitochondria induces the defect in autophagy. From proteome analyses, the authors hypothesized that autophagy is impacted by the abundance of eIF2β and the phosphorylation of eIF2α. The authors followed up the proteome analyses by testing the effects of eIF2β overexpression and depletion on autophagy. With the results from those experiments, the authors proposed a novel role of eIF2β in proteostasis that underlies neurodegeneration derived from the depletion of axonal mitochondria.

The manuscript has several weaknesses. The reader should take extra care while reading this manuscript and when acknowledging the findings and the model in this manuscript.

The defect in autophagy by the depletion of axonal mitochondria is one of the main claims in the paper. The authors should work more on describing their results of LC3-II/LC3-I ratio, as there are multiple ways to interpret the LC3 blotting for the autophagy assessment. Lysosomal defects result in the accumulation of LC3-II thus the LC3-II/LC3-I ratio gets higher. On the other hand, the defect in the early steps of autophagosome formation could result in a lower LC3-II/LC3-I ratio. From the results of the actual blotting, the LC3-I abundance is the source of the major difference for all conditions (Milton RNAi and eIF2β overexpression and depletion). In the text, the authors simply state the observation of their LC3 blotting. The manuscript lacks an explanation of how to evaluate the LC3-II/LC3-I ratio. Also, the manuscript lacks an elaboration on what the results of the LC3 blotting indicate about the state of autophagy by the depletion of axonal mitochondria.

Thank you for pointing it out, and we apologize for an insufficient description of the result. We included quantitation of the levels of LC3-I and LC3-II in Figure 2A, 2D, 3D, 6B and 7B. As the reviewer pointed out, changes in the LC3-II/LC3-I ratio do not necessarily indicate autophagy defects. However, since p62 accumulation (Figure 2B, 2E, 3E, 6C, 7C in the original manuscript), these results collectively suggest that autophagy is lowered. We revised the manuscript to include this discussion as below:

Lines 174-186 ‘During autophagy progression, LC3 is conjugated with phosphatidylethanolamine to form LC3-II, which localizes to isolation membranes and autophagosomes. LC3-I accumulation occurs when autophagosome formation is impaired, and LC3-II accumulation is associated with lysosomal defects(31,32). p62 is an autophagy substrate, and its accumulation suggests autophagic defects(31,32). We found that milton knockdown increased LC3-I, and the LC3-II/LC3-I ratio was lower in milton knockdown flies than in control flies at 14-day-old (Figure 2A). We also analyzed p62 levels in head lysates sequentially extracted using detergents with different stringencies (1% Triton X-100 and 2% SDS). Western blotting revealed that p62 levels were increased in the brains of 14-day-old of milton knockdown flies (Figure 2B). The increase in the p62 level was significant in the Triton X-100-soluble fraction but not in the SDS-soluble fraction (Figure 2B), suggesting that depletion of axonal mitochondria impairs the degradation of less-aggregated proteins.’

Line 189-190 : ‘At 30 day-old, LC3-I was still higher, and the LC3-II/LC3-I ratio was lower, in milton knockdown compared to the control (Figure 2D).’

Line 199-201: ‘However, in contrast with milton knockdown, Pfk knockdown did not affect the levels of LC3-I, LC3-II or the LC3-II/LC3-I ratio (Figure 3D).’

Line 275-281: ‘Neuronal overexpression of eIF2β increased LC3-II, while the LC3-II/LC3-I ratio was not significantly different (Figure 6A and B). Overexpression of eIF2β significantly increased the p62 level in the Triton X-100-soluble fraction (Figure 6C, 4-fold vs. control, p < 0.005 (1% Triton X-100)) but not in the SDS-soluble fraction (Figure 6C, 2-fold vs. control, p = 0.062 (2% SDS)), as observed in brains of milton knockdown flies (Figure 2B). These data suggest that neuronal overexpression of eIF2β accumulates autophagic substrates.’

Line 307-315: ‘Neuronal knockdown of milton causes accumulation of autophagic substrate p62 in the Triton X-100-soluble fraction (Figure 2B), and we tested if lowering eIF2β ameliorates it. We found that eIF2β heterozygosity caused a mild increase in LC3-I levels and decreases in LC3-II levels, resulting in a significantly lower LC3-II/LC3-I ratio in milton knockdown flies (Figure 7B). eIF2β heterozygosity decreased the p62 level in the Triton X-100-soluble fraction in the brains of milton knockdown flies (Figure 7C). The p62 level in the SDS-soluble fraction, which is not sensitive to milton knockdown (Figure 2B), was not affected (Figure 7C). These results suggest that suppression of eIF2β ameliorates the impairment of autophagy caused by milton knockdown.’

Another main point of the paper is the up-regulation of eIF2β by depleting the axonal mitochondria leads to the proteostasis crisis. This claim is formed by the findings from the proteome analyses. The authors should have presented their proteomic data with much thorough presentation and explanation. As in the experiment scheme shown in Figure 4A, the author did two proteome analyses: one from the 7-day-old sample and the other from the 21-day-old sample. The manuscript only shows a plot of the result from the 7-day-old sample, but that of the result from the 21-day-old sample. For the 21-day-old sample, the authors only provided data in the supplemental table, in which the abundance ratio of eIF2β from the 21-day-old sample is 0.753, meaning eIF2β is depleted in the 21-day-old sample. The authors should have explained the impact of the eIF2β depletion in the 21-day-old sample, so the reader could fully understand the authors' interpretation of the role of eIF2β on proteostasis.

Thank you for pointing it out. We included plots of the results of 21-day-old proteome as a part of the main figure (Figure 4C). As the reviewer pointed out, eIF2β protein levels are reduced at the 21-day-old. Since a reduction in the eIF2_β_ ameliorated milton knockdown-induced locomotor defects in aged flies (Figure 7D), the reduction in eIF2β observed in the 21-day-old milton knockdown flies is not likely to negatively contribute to milton knockdown-induced defects. We included this discussion in the manuscript as below:

Lines 337-341:‘eIF2β protein levels are reduced at the 21-day-old; however, since a reduction in the eIF2β ameliorated milton knockdown-induced locomotor defects in aged flies (Figure 7), the reduction in eIF2β observed in the 21-day-old is not likely to negatively contribute to milton knockdown-induced defects.’

The manuscript consists of several weaknesses in its data and explanation regarding translation.

(1) The authors are likely misunderstanding the effect of phosphorylation of eIF2α on translation. The P-eIF2α is inhibitory for translation initiation. However, the authors seem to be mistaken that the down-regulation of P-eIF2α inhibits translation.

We are sorry for our insufficient explanation in the previous version. As the reviewer pointed out, it is well known that the phosphorylated form of eIF2α inhibits translation initiation. Neuronal knockdown of milton caused a reduction in p-eIF2α (Figure 4J and K), and it also lowered translation (Figure 5); the relationship between these two events is currently unclear. We do not think that a reduction in the p-eIF2α suppressed translation; rather, we propose that the unbalance of expression levels of the components of eIF2 complexes negatively affects translation. We revised discussion sections to describe our interpretation more in detail as below:

Line 368-378: ‘eIF2β is a component of eIF2, which meditates translational regulation and ISR initiation. When ISR is activated, phosphorylated eIF2α suppresses global translation and induces translation of ATF4, which mediates transcription of autophagy-related genes(39,40). Since ISR can positively regulate autophagy, we suspected that suppression of ISR underlies a reduction in autophagic protein degradation. We found neuronal knockdown of milton reduced phosphorylated eIF2α, suggesting that ISR is reduced (Figure 4). However, we also found that global translation was reduced (Figure 5). It may be possible that increased levels of eIF2β disrupt the eIF2 complex or alter its functions. The stoichiometric mismatch caused by an imbalance of eIF2 components may inhibit ISR induction. Supporting this model, we found that eIF2β upregulation reduced the levels of p-eIF2α (Figure 6).’

We have revised the graphical abstract and removed the eIF2 complex since its role in the loss of proteostasis caused by milton knockdown has not been elucidated yet.

(2) The result of polysome profiling in Figure 4H is implausible. By 10%-25% sucrose density gradient, polysomes are not expected to be observed. The authors should have used a gradient with much denser sucrose, such as 10-50%.

Thank you for pointing it out. It was a mistake of 10-50%, and we apologize for the oversight. It was corrected (Figure 5).

(3) Also on the polysome profiling, as in the method section, the authors seemed to fractionate ultra-centrifuged samples from top to bottom and then measured A260 by a plate reader. In that case, the authors should have provided a line plot with individual data points, not the smoothly connected ones in the manuscript.

Thank you for pointing it out. We revised the graph (Figure 5).

(4) For both the results from polysome profiling and puromycin incorporation (Figure 4H and I), the difference between control siRNA and Milton siRNA are subtle, if not nonexistent. This might arise from the lack of spatial resolution in their experiment as the authors used head lysate for these data but the ratio of Phospho-eIF2α/eIF2α only changes in the axons, based on their results in Figure 4E-G. The authors could have attempted to capture the spatial resolution for the axonal translation to see the difference between control siRNA and Milton siRNA.

Thank you for your comment. We agree that it would be an interesting experiment, but it will take a considerable amount of time to analyze axonal translation with spatial resolution. We will try to include such analyses in the future. For this manuscript, we revised the discussion section to include the reviewer's suggestion as below;

Lines 351-353: ‘Further analyses to dissect the effects of milton knockdown on proteostasis and translation in the cell body and axon by experiments with spatial resolution would be needed.’

Recommendations for the authors:

From the Reviewing Editor:

As the Reviewing Editor, I have read your manuscript and the associated peer reviews. I have concerns about publishing this work in its current form. I think that your manuscript cannot claim to have found a novel function of eIF2beta because of technical uncertainties and conceptual problems that should be addressed.

Thank you so much for your review and comments. We addressed all the concerns raised by the reviewers. Point-by-point responses are listed below.

First, your manuscript is based partly on what appears to be a mistaken understanding of the mechanistic basis of the ISR. Specifically, eIF2 is a heterotrimeric complex of alpha, beta, and gamma subunits. When eIF2a is phosphorylated, the heterotrimer adopts a new conformation. This conformation directly binds and inhibits eIF2B, the decameric GEF that exchanges the GDP bound to the gamma subunit of the eIF2 complex for GTP. Unless I misunderstood your paper, you seem to propose that decreasing levels of phospho-eIF2a will inhibit translation, but this is backward from what we know about the ISR.

Thank you for your insightful comment, and we are sorry for the confusion. We did not mean to propose that decreasing levels of phospho-eIF2_a_ inhibits translation. We apologize for our insufficient explanation, which might have caused a misunderstanding (Lines 312-318 in the original version). We agree with the reviewer that ‘mismatch due to elevated eIF2-beta could change the behavior of the ISR’. We revised the text in the result section as follows:

Lines 259-264 (in the Result section) ‘Phosphorylation of eIF2α induces conformational changes in the eIF2 complex and inhibits global translation(36). To analyze the effects of milton knockdown on translation, we performed polysome gradient centrifugation to examine the level of ribosome binding to mRNA. Since p-eIF2α was downregulated, we hypothesized that milton knockdown would enhance translation. However, unexpectedly, we found that milton knockdown significantly reduced the level of mRNAs associated with polysomes (Figure 5A and B).’

Lines 368-378 (in the Discussion section): ‘eIF2β is a component of eIF2, which meditates translational regulation and ISR initiation. When ISR is activated, phosphorylated eIF2α suppresses global translation and induces translation of ATF4, which mediates transcription of autophagy-related genes(39,40). Since ISR can positively regulate autophagy, we suspected that suppression of ISR underlies a reduction in autophagic protein degradation. We found neuronal knockdown of milton reduced phosphorylated eIF2α, suggesting that ISR is reduced (Figure 4). However, we also found that global translation was reduced (Figure 5). It may be possible that increased levels of eIF2β disrupt the eIF2 complex or alter its functions. The stoichiometric mismatch caused by an imbalance of eIF2 components may inhibit ISR induction. Supporting this model, we found that eIF2β upregulation reduced the levels of p-eIF2α (Figure 6).’

It may be possible that a stoichiometric mismatch due to elevated eIF2-beta could change the behavior of the ISR, but your paper doesn't adequately address the expression levels of all three eIF2 subunits: alpha, beta, and gamma. The proteomic data shown in Fig 4B is unconvincing on its own because the changes in the beta subunit are subtle. The Western blot in Figure 4C suggests that the KD changes the mass or mobility of the beta subunit, and most importantly, there are no Western blots measuring the levels of eIF2a, eIF2a-phospho, or eIF2-gamma.

We appreciate the reviewer’s comment and agree that the stoichiometric mismatch due to elevated eIF2β may interfere with ISR. We found overexpression of eIF2β lowered p-eIF2 alpha (Figure S2 in V1), which supports this model. We included this data in the main figure in the revised manuscript (Figure 6D) and revised the text as below:

Lines 279-281: ‘Since milton knockdown reduced the p-eIF2α level (Figure 4K), we asked whether an increase in eIF2β affects p-eIF2α. Neuronal overexpression of eIF2β did not affect the eIF2α level but significantly decreased the p-eIF2α level (Figure 6D, E).’

Expression data of eIF2α and eIF2γ from proteomic analyses has been extracted from proteome analyses and included as a table (Figure 4D). Western blots of phospho-eIF2a (Figure S1 in V1) in the main figure (Figure 4G). The result section was revised as below;

Lines 242-245: ‘As for the other subunits of eIF2 complex, proteome analysis did not detect a significant difference in the protein levels of eIF2α and eIF2γ between milton knockdown and control flies at 7 and 21 days (Figure 4D).’

Reviewer #1 (Recommendations For The Authors):

L125-128: In this section, while the efficiency of Milton knockdown is referenced from a previous publication, it is necessary to also mention that the Miro knockdown has been similarly reported in the literature. Additionally, the Methods section lacks details on the Miro RNAi line used, and Table 2 does not include the genotype for Miro RNAi. This information should be included for clarity and completeness.

Thank you for pointing it out. Knockdown efficiency with this strain has been reported (Iijima-Ando et al., PLoS Genet, 2012). We revised the text to include citation and knockdown efficiency as follows:

Lines 139-147: ‘There was no significant increase in ubiquitinated proteins in milton knockdown flies at 1-day old, suggesting that the accumulation of ubiquitinated proteins caused by milton knockdown is age-dependent (Figure S1). We also analyzed the effect of the neuronal knockdown of Miro, a partner of milton, on the accumulation of ubiquitin-positive proteins. Since severe knockdown of Miro in neurons causes lethality, we used UAS-Miro RNAi strain with low knockdown efficiency, whose expression driven by elav-GAL4 caused 30% reduction of Miro mRNA in head extract(24). Although there was a tendency for increased ubiquitin-positive puncta in Miro knockdown brains, the difference was not significant (Figure 1B, p>0.05 between control RNAi and Miro RNAi). These data suggest that the depletion of axonal mitochondria induced by milton knockdown leads to the accumulation of ubiquitinated proteins before neurodegeneration occurs.’

L132-L136: The current phrasing in this section suggests an increase in ubiquitinated proteins for both Milton and Miro knockdowns. However, since there is no significant difference noted for Miro, it is incorrect to state an increase in ubiquitin-positive puncta. Furthermore, combining the results of Milton knockdown to claim an increase in ubiquitinated proteins prior to neurodegeneration is misleading. At the very least, the expression here needs to be moderated to accurately reflect the findings.

Thank you for pointing it out. We revised the text as above.

L137-L141: Results in Figure 1 indicate that Milton knockdown leads to an increase in ubiquitinated proteins at 14 days, while Miro knockdown shows no difference from the control at either 14 or 30 days. Conversely, both the control and Miro exhibit an increase in ubiquitinated proteins with aging, but this trend does not seem to apply to Milton knockdown. This observation suggests that Milton KD may not affect the changes in protein quality control associated with aging. It implies that Milton's function might be more related to protein homeostasis in younger cells, or that changes due to aging might overshadow the effects of Milton knockdown. These interpretations should be included in the Results or Discussion sections for a more comprehensive analysis.

Thank you for your insightful comment. We revised the text to include those points as follows:

Lines 152-153: ‘These results suggest that depletion of axonal mitochondria may have more impact on proteostasis in young neurons than in old neurons.’

Lines 355-362: ‘The depletion of axonal mitochondria and accumulation of abnormal proteins are both characteristics of aged brains(37,38). Our results suggest that the loss of axonal mitochondria is an event upstream of proteostasis collapse during aging. Neuronal knockdown of milton had more impact on proteostasis in young neurons than the old neurons (Figure 1). Proteome analyses also showed that age-related pathways, such as immune responses, are enhanced in young flies with milton knockdown (Table 2). The reduction in axonal transport of mitochondria may be one of the triggering events of age-related changes and accelerates the onset of aging in the brain.’

L143 : Please remove the erroneously included quotation mark.

Thank you for pointing it out. We corrected it.

L145-L147:

- While it is understood that Milton knockdown results in a reduction of mitochondria in axons, as reported previously and seemingly indicated in Figure 1E, this paper repeatedly refers to axonal depletion of mitochondria. Therefore, it would be beneficial to quantitatively assess the number of mitochondria in the axonal terminals located in the lamina via electron microscopy. Such quantification would robustly reinforce the argument that mitochondrial absence in axons is a consequence of Milton knockdown.

Thank you for pointing it out. We included quantitation of the number of mitochondria in the synaptic terminals (Figure 1E).

The text and figure legend was revised accordingly:

Lines 156-157: ‘As previously reported(24), the number of mitochondria in presynaptic terminals decreased in milton knockdown (Figure 1E).’

- The knockdown of Milton is known to reduce mitochondrial transport from an early stage, but what about swelling? By observing swelling at 1 day and 14 days, it may be possible to confirm the onset of swelling and discuss its correlation with the accumulation of ubiquitinated proteins.

Quantitation of axonal swelling has also been included (Figure 1F).

We appreciate reviewer’s comments on the correlation between the accumulation of ubiquitinated proteins and axonal swelling. Axonal swelling was not observed at 3-days-old (Iijima-Ando et al., PLoS Genetics, 2012), indicating that axonal swelling is an age-dependent event. Dense materials are found in swollen axons more often than in normal axons, suggesting a positive correlation between disruption of proteostasis and axonal damage. It would be interesting to analyze the time course of events further; however, we feel it is beyond the scope of this manuscript. We revised the text as below to include this discussion:

Lines 157-159: ‘The swelling of presynaptic terminals, characterized by the enlargement and roundness, was not reported at 3-day-old(24) but observed at this age with about 4% of total presynaptic terminals (Figure 1F, asterisks).’

Lines 162-167: ‘Dense materials are rarely found in age-matched control neurons, indicating that milton knockdown induces abnormal protein accumulation in the presynaptic terminals (Figure 1G and H). In milton knockdown neurons, dense materials are found in swollen presynaptic terminals more often than in presynaptic terminals without swelling, suggesting a positive correlation between the disruption of proteostasis and axonal damage (Figure 1G).’

Lines 362-365: ‘Disruption of proteostasis is expected to contribute neurodegeneration(38), and it would be interesting to analyze the sequence of protein accumulation and axonal degeneration in milton knockdown ((24,29) and Figure 1) in detail with higher time resolution.’

L147-L151: Though Figures 1F and 1G provide qualitative representations, it is advisable to quantitatively assess whether dense materials significantly accumulate. Such quantitative analysis would be required to verify the accumulation of dense materials in the context of the study.

Thank you for pointing it out. We included quantitation of the number of neurons with dense material (Figure 1G). We revised the manuscript as follows:

Line 161-163: ‘Dense materials are rarely found in age-matched control neurons, indicating that milton knockdown induces abnormal protein accumulation in the presynaptic terminals (Figure 1G and H).’

Regarding Figure 1B, C:

- Even though the count of puncta in the whole brain appears to be fewer than 400, the magnification of the optic lobe suggests a substantial presence of puncta. Please clarify in the Methods section what constitutes a puncta and whether the quantification in the whole brain is based on a 2D or 3D analysis. Detail the methodology used for quantification.

Thank you for your comment. We revised the method section to include more details as below:

Lines 434-437: ‘Quantitative analysis was performed using ImageJ (National Institutes of Health) with maximum projection images derived from Z-stack images acquired with same settings. Puncta was identified with mean intensity and area using ImageJ.’

- What about 1-day-old specimens? Does Milton knockdown already show an increase in ubiquitinated protein accumulation at this early stage? Investigating whether ubiquitin-protein accumulation is involved in aging promotion or is already prevalent during developmental stages is a necessary experiment.

Thank you for your comment. We carried out immunostaining with an anti-ubiquitin antibody in the brains at 1-day-old. No significant difference was detected between the control and milton knockdown. This result has been included as Figure S1 in the revised manuscript. The result section was revised as below:

Line 136-139 ‘There was no significant increase in ubiquitinated proteins in milton knockdown flies at 1-day old, suggesting that the accumulation of ubiquitinated proteins caused by milton knockdown is age-dependent (Figure S1).’

For Figure 1E: In the Electron Microscopy section of the Methods, define how swollen axons were identified and describe the quantification methodology used.

Thank you for your comment. Swollen axons are, unlike normal axons, round in shape and enlarged. We revised the text as below;

Lines 157-160: ‘The swelling of presynaptic terminals, characterized by the enlargement and roundness, was not reported at 3-day-old(24) but observed at this age with about 4% of total presynaptic terminals (Figure 1F, asterisks).’

Lines 683-684, Figure 1 legend: ‘Swollen presynaptic terminals (asterisks in (F)), characterized by the enlargement and higher circularity, were found more frequently in milton knockdown neurons.’

L218-L219: Throughout the text, the expression 'eIF2β is "upregulated" in response to Milton knockdown' is frequently used. However, considering the presented results, it might be more accurate to interpret that under the condition of Milton knockdown, eIF2β is not undergoing degradation but rather remains stable.

Thank you for pointing it out. We replaced ‘upregulated’ with ‘increased’ throughout the text.

L234-L235: On what basis is the conclusion drawn that there is a reduction? Given that three experiments have been conducted, it would be possible and more convincing to quantify the results to determine if there is a significant decrease.

Thank you for pointing it out. We quantified the AUC of polysome fraction and carried out statistical analysis. There is a significant decrease in polysome in milton knockdown, and this result has been included in Figure 5B. We revised the figure and the legend accordingly.

L236: 5H-> 4H

Thank you for pointing it out, and we are sorry for the confusion. We corrected it.

L238-L239: Since there is no significant difference observed, it may not be accurate to interpret a reduction in puromycin incorporation.

Thank you for pointing it out. As described above, quantification of polysome fractions showed that milton knockdown significantly reduce polysome (Figure 5B). We revised the manuscript as below;

Lines 263-264: ‘However, unexpectedly, we found that milton knockdown significantly reduced the level of mRNAs associated with polysomes (Figure 5A and B).’

Figure 5D and Figure 6D: Climbing assays have been conducted, but I believe experiments should also be performed to examine whether overexpression or heterozygous mutants of eIF2β induce or suppress degeneration.

Thank you for pointing it out. We analyzed the eyes with eIF2_β_ overexpression for neurodegeneration. Although there was a tendency of elevated neurodegeneration in the retina with eIF2_β_ overexpression, the difference between control and eIF2_β_ overexpression did not reach statistical significance (Figure S2). This result has been included as Figure S2 in the revised manuscript, and the following sentences have been included in the text:

Lines 288-293: ‘We asked if eIF2β overexpression causes neurodegeneration, as depletion of axonal mitochondria in the photoreceptor neurons causes axon degeneration in an age-dependent manner(24). eIF2β overexpression in photoreceptor neurons tends to increase neurodegeneration in aged flies, while it was not statistically significant (p>0.05, Figure S2).’

L271-L272: The results in Figure 6B are surprising. I anticipated a greater increase compared to the Milton knockdown alone. While p62 appears to be reduced, it is not clear why these results lead to the conclusion that lowering eIF2β rescues autophagic impairment. Please add a discussion section to address this point.

Thank you for pointing it out. We apologize for the unclear description of the result. Milton knockdown flies show p62 accumulation (Figure 2), and deleting one copy of eIF2beta in milton knockdown background reduced p62 accumulation (Figure 7C). We revised the text as below:

Lines 307-315: ‘Neuronal knockdown of milton causes accumulation of autophagic substrate p62 in the Triton X-100-soluble fraction (Figure 2B), and we tested if lowering eIF2β ameliorates it. We found that eIF2β heterozygosity caused a mild increase in LC3-I levels and decreases in LC3-II levels, resulting in a significantly lower LC3-II/LC3-I ratio in milton knockdown flies (Figure 7B). eIF2β heterozygosity decreased the p62 level in the Triton X-100-soluble fraction in the brains of milton knockdown flies (Figure 7C). The p62 level in the SDS-soluble fraction, which is not sensitive to milton knockdown (Figure 2B), was not affected (Figure 7C). These results suggest that suppression of eIF2β ameliorates the impairment of autophagy caused by milton knockdown.’

L369: Please specify the source of the anti-ubiquitin antibody used.

Thank you for pointing it out. We included the antibody information in the method section.

Figure 7: While the relationship between Milton knockdown and the eIF2β and eIF2α proteins has been elucidated through the authors' efforts, I would like to see an investigation into whether eIF2β is upregulated and eIF2α phosphorylation is reduced in simply aged Drosophila. This would help us understand the correlation between aging and eIF2 protein dynamics.

Thank you for your comment. We agree that it is an important question, and we are working on it. However, we feel that it is beyond the scope of the current manuscript.

L645-L646: If the mushroom body is identified using mito-GFP, then include mito-GFP in the genotype listed in Supplementary Table 2.

We are sorry for the oversight. We corrected it in Supplementary Table 2.

Additionally, while it is presumed that the mito-GFP signal decreases in axons with Milton RNAi, how was the lobe tips area accurately selected for analysis? Please include these details along with a comprehensive description of the quantification methodology in the Methods section.

Thank you for your comment. Although the mito-GFP signal in the axon is weak in the milton knockdown neurons, it is sufficient to distinguish the mushroom body structure from the background. We revised the method section to include this information in the method section:

Line 437-438: ‘For eIF2α and p-eIF2α immunostaining, the mushroom body was detected by mitoGFP expression.’

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this work, the authors present a cornucopia of data generated using deep mutational scanning (DMS) of variants in MET kinase, a protein target implicated in many different forms of cancer. The authors conducted a heroic amount of deep mutational scanning, using computational structural models to augment the interpretation of their DMS findings.

Strengths:

This powerful combination of computational models, experimental structures in the literature, dose-response curves, and DMS enables them to identify resistance and sensitizing mutations in the MET kinase domain, as well as consider inhibitors in the context of the clinically relevant exon-14 deletion. They then try to use the existing language model ESM1b augmented by an XGBoost regressor to identify key biophysical drivers of fitness. The authors provide an incredible study that has a treasure trove of data on a clinically relevant target that will appeal to many.

We thank Reviewer 1 for their generous assessment of our manuscript!

Weaknesses:

However, the authors do not equally consider alternative possible mechanisms of resistance or sensitivity beyond the impact of mutation on binding, even though the measure used to discuss resistance and sensitivity is ultimately a resistance score derived from the increase or decrease of the presence of a variant during cell growth.

For this resistance screen, Ba/F3 was a carefully chosen cellular selection system due to its addiction to exogenously provided IL-3, undetected expression of endogenous RTKs (including MET), and dependence on kinase transgenes to promote signaling and growth under IL-3 withdrawal. Together this allows for the readout of variants that alter kinase-driven proliferation without the caveat of bypass resistance. In our previous phenotypic screen (Estevam et al., 2024, eLife), we also carefully examined the impact of all possible MET kinase domain mutations both in the presence and absence of IL-3 withdrawal, but no inhibitors. There, we identified a small group of mutations that were associated with gain-of-function behavior located at conserved regulatory motifs outside of the catalytic site, yet these mutations were largely sensitive to inhibitors within this screen.

Here, the majority of resistance mutations were located at or near the ATP-binding pocket, suggesting an impact on resistance through direct drug interactions. However, there was also a small population of distal mutations that met our statistical definitions of resistance. Within the crizotinib selection, sites such as T1293, L1272, T1261, amongst others, demonstrated resistance profiles but were located in C-lobe away from the catalytic site. While we did not experimentally validate these specific mutations, it is possible that non-direct drug binders instead promote resistance through allosteric or conformational mechanisms which preserve kinase activity and signaling. Indeed, our ML framework explicitly included conformational and stability effects as significant in improving predictions.

We would be happy to further discuss any specific alternative resistance mechanisms Reviewer 1 has in mind! Thank you for highlighting this!

There are also points of discussion and interpretation that rely heavily on docked models of kinase-inhibitor pairs without considering alternative binding modes or providing any validation of the docked pose. Lastly, the use of ESM1b is powerful but constrained heavily by the limited structural training data provided, which can lead to misleading interpretations without considering alternative conformations or poses.

The majority of our interpretations are grounded in the X-ray structures of WT MET bound to the inhibitors studied (or close analogs). The use of docked models (note - to mutant structures predicted by UMol, not ESM, that can have conformational changes) is primarily in the ML part of the manuscript. Indeed, in our models, conformational and binding mode changes are taken into account as features (see Ligand RMSD, Residue RMSD). There are certainly improved methods (AF3 variants) emerging that might have even more power to model these changes, but they come with greater computational costs and are something we will be evaluating in the future.

We added to the results section: “While our features can account for some changes in MET-mutant conformation and altered inhibitor binding pose, the prediction of these aspects can likely be improved with new methods.”

Reviewer #2 (Public review):

Summary:

This manuscript provides a comprehensive overview of potential resistance mutations within MET Receptor Tyrosine Kinase and defines how specific mutations affect different inhibitors and modes of target engagement. The goal is to identify inhibitor combinations with the lowest overlap in their sensitivity to resistant mutations and determine if certain resistance mutations/mechanisms are more prevalent for specific modes of ATP-binding site engagement. To achieve this, the authors measured the ability of ~6000 single mutants of MET's kinase domain (in the context of a cytosolic TPR fusion) to drive IL-3-independent proliferation (used as a proxy for activity) of Ba/F3 cells (deep mutational profiling) in the presence of 11 different inhibitors. The authors then used co-crystal and docked structures of inhibitor-bound MET complexes to define the mechanistic basis of resistance and applied a protein language model to develop a predictive model of inhibitor sensitivity/resistance.

Strengths:

The major strengths of this manuscript are the comprehensive nature of the study and the rigorous methods used to measure the sensitivity of ~6000 MET mutants in a pooled format. The dataset generated will be a valuable resource for researchers interested in understanding kinase inhibitor sensitivity and, more broadly, small molecule ligand/protein interactions. The structural analyses are systematic and comprehensive, providing interesting insights into resistance mechanisms. Furthermore, the use of machine learning to define inhibitor-specific fitness landscapes is a valuable addition to the narrative. Although the ESM1b protein language model is only moderately successful in identifying the underlying mechanistic basis of resistance, the authors' attempt to integrate systematic sequence/function datasets with machine learning serves as a foundation for future efforts.

We thank Reviewer 2 for their thoughtful assessment of our manuscript!

Weaknesses:

The main limitation of this study is that the authors' efforts to define general mechanisms between inhibitor classes were only moderately successful due to the challenge of uncoupling inhibitor-specific interaction effects from more general mechanisms related to the mode of ATP-binding site engagement. However, this is a minor limitation that only minimally detracts from the impressive overall scope of the study.

We agree. We have added to the discussion: “A full landscape of mutational effects can help to predict drug response and guide small molecule design to counteract acquired resistance. The ability to define molecular mechanisms towards that goal will likely require more purposefully chosen chemical inhibitors and combinatorial mutational libraries to be maximally informative.”

Reviewer #3 (Public review):

Summary:

In the manuscript 'Mapping kinase domain resistance mechanisms for the MET receptor tyrosine kinase via deep mutational scanning' by Estevam et al, deep mutational scanning is used to assess the impact of ~5,764 mutants in the MET kinase domain on the binding of 11 inhibitors. Analyses were divided by individual inhibitor and kinase inhibitor subtypes (I, II, I 1/2, and III). While a number of mutants were consistent with previous clinical reports, novel potential resistance mutants were also described. This study has implications for the development of combination therapies, namely which combination of inhibitors to avoid based on overlapping resistance mutant profiles. While one suggested pair of inhibitors with the least overlapping resistance mutation profiles was suggested, this manuscript presents a proof of concept toward a more systematic approach for improved selection of combination therapeutics. Furthermore, in a final part of this manuscript the data was used to train a machine learning model, the ESM-1b protein language model augmented with an XG Boost Regressor framework, and found that they could improve predictions of resistance mutations above the initial ESM-1b model.

Strengths:

Overall this paper is a tour-de-force of data collection and analysis to establish a more systematic approach for the design of combination therapies, especially in targeting MET and other kinases, a family of proteins significant to therapeutic intervention for a variety of diseases. The presentation of the work is mostly concise and clear with thousands of data points presented neatly and clearly. The discovery of novel resistance mutants for individual MET inhibitors, kinase inhibitor subtypes within the context of MET, and all resistance mutants across inhibitor subtypes for MET has clinical relevance. However, probably the most promising outcome of this paper is the proposal of the inhibitor combination of Crizotinib and Cabozantib as Type I and Type II inhibitors, respectively, with the least overlapping resistance mutation profiles and therefore potentially the most successful combination therapy for MET. While this specific combination is not necessarily the point, it illustrates a compelling systematic approach for deciding how to proceed in developing combination therapy schedules for kinases. In an insightful final section of this paper, the authors approach using their data to train a machine learning model, perhaps understanding that performing these experiments for every kinase for every inhibitor could be prohibitive to applying this method in practice.

We thank Reviewer 3 for their assessment of our manuscript (we are very happy to have it described as a tour-de-force!)

Weaknesses:

This paper presents a clear set of experiments with a compelling justification. The content of the paper is overall of high quality. Below are mostly regarding clarifications in presentation.

Two places could use more computational experiments and analysis, however. Both are presented as suggestions, but at least a discussion of these topics would improve the overall relevance of this work. In the first case it seems that while the analyses conducted on this dataset were chosen with care to be the most relevant to human health, further analyses of these results and their implications of our understanding of allosteric interactions and their effects on inhibitor binding would be a relevant addition. For example, for any given residue type found to be a resistance mutant are there consistent amino acid mutations to which a large or small or effect is found. For example is a mutation from alanine to phenylalanine always deleterious, though one can assume the exact location of a residue matters significantly. Some of this analysis is done in dividing resistance mutants by those that are near the inhibitor binding site and those that aren't, but more of these types of analyses could help the reader understand the large amount of data presented here. A mention at least of the existing literature in this area and the lack or presence of trends would be worthwhile. For example, is there any correlation with a simpler metric like the Grantham score to predict effects of mutations (in a way the ESM-1b model is a better version of this, so this is somewhat implicitly discussed).

Indeed we experimented with including these types of features in the XGBoost scheme (particularly residue volume change and distance) to augment the predictive power of the ESM model - see Figure 8 - figure supplement 1; however, we didn’t find them as significant. Therefore, the signal is likely very small and/or incorporated into the baseline ESM model.

Indeed, this discussion relates to the second point this manuscript could improve upon: the machine learning section. The main actionable item here is that this results section seems the least polished and could do a better job describing what was done. In the figure it looks like results for certain inhibitors were held out as test data - was this all mutants for a single inhibitor, or some other scheme? Overall I think the implications of this section could be fleshed out, potentially with more experiments.

Figure 8A and the methods section contain a very detailed explanation of test data. We have thought about it and do not have any easy path to improve the description, which we reproduce here:

“Experimental fitness scores of MET variants in the presence of DMSO and AMG458 were ignored in model training and testing since having just one set of data for a type I ½ inhibitor and DMSO leads to learning by simply memorizing the inhibitor type, without generalizability. The remaining dataset was split into training and test sets to further avoid overfitting (Figure 8A). The following data points were held out for testing - (a) all mutations in the presence of one type I (crizotinib) and one type II (glesatinib analog) inhibitor, (b) 20% of randomly chosen positions (columns) and (c) all mutations in two randomly selected amino acids (rows) (e.g. all mutations to Phe, Ser). After splitting the dataset into train and test sets, the train set was used for XGBoost hyperparameter tuning and cross-validation. For tuning the hyperparameters of each of the XGBoost models, we held out 20% of randomly sampled data points in the training set and used the remaining 80% data for Bayesian hyperparameter optimization of the models with Optuna (Akiba et al., 2019), with an objective to minimize the mean squared error between the fitness predictions on 20% held out split and the corresponding experimental fitness scores. The following hyperparameters were sampled and tuned: type of booster (booster - gbtree or dart), maximum tree depth (max_depth), number of trees (n_estimators), learning rate (eta), minimum leaf split loss (gamma), subsample ratio of columns when constructing each tree (colsample_bytree), L1 and L2 regularization terms (alpha and beta) and tree growth policy (grow_policy - depthwise or lossguide). After identifying the best combination of hyperparameters for each of the models, we performed 10-fold cross validation (with re-sampling) of the models on the full training set. The training set consists of data points corresponding to 230 positions and 18 amino acids. We split these into 10 parts such that each part corresponds to data from 23 positions and 2 amino acids. Then, at each of 10 iterations of cross-validation, models were trained on 9 of 10 parts (207 positions and 16 amino acids) and evaluated on the 1 held out part (23 positions and 2 amino acids). Through this protocol we ensure that we evaluate performance of the models with different subsets of positions and amino acids. The average Pearson correlation and mean squared error of the models from these 10 iterations were calculated and the best performing model out of 8192 models was chosen as the one with the highest cross-validation correlation. The final XGBoost models were obtained by training on the full training set and also used to obtain the fitness score predictions for the validation and test sets. These predictions were used to calculate the inhibitor-wise correlations shown in Figure 8B.“

As mentioned in the 'Strengths' section, one of the appealing aspects of this paper is indeed its potential wide applicability across kinases -- could you use this ML model to predict resistance mutants for an entirely different kinase? This doesn't seem far-fetched, and would be an extremely compelling addition to this paper to prove the value of this approach.

This is exactly where we want to go next! But as we see here, it is going to be hard and require more purposeful selection of chemicals and likely combinatorial mutations to be maximally informative (see also reviewer 2 response where we have added text)

Another area in which this paper could improve its clarity is in the description of caveats of the assay. The exact math used to define resistance mutants and its dependence on the DMSO control is interesting, it is worth discussing where the failure modes of this procedure might be. Could it be that the resistance mutants identified in this assay would differ significantly from those found in patients? That results here are consistent with those seen in the clinic is promising, but discrepancies could remain.

Thank you for pointing this out. The greatest trade-off of probing the intracellular MET kinase (juxtamembrane, kinase domain, c-tail) in the constitutively active TPR system is that while we gain cytoplasmic expression, constitutive oligomerization, and HGF-independent activation, other features like membrane-proximal effects are lost and translatability of some mutations in non-proliferative conditions may also be limited. Nevertheless, Ba/F3 allows IL-3 withdrawal to serve as an effective variant readout of transgenic kinase variant effects due to its undetectable expression of endogenous RTKs and addiction to exogenous interleukin-3 (IL-3).

In our previous study, we were also interested in comparing the phenotypic results to available patient populations in cBioPortal. We observed that our DMS captured known oncogenic MET kinase variants, in addition to a population of gain-of-function variants within clinical residue positions that have not been clinically reported. Interestingly, the population of possible novel gain-of-function mutant codons were more distant in genetic space (2-3 Hamming distance) from wild type than the clinically reported variant codon (1-2 Hamming distance).

For this inhibitor screen, we also carefully compared previously reported and validated resistance mutations across referenced publications to that of our inhibitor screen, and observed large agreement as noted in-text. While discrepancies could definitely remain, there is precedence for consistency.

Furthermore a more in depth discussion of the MetdelEx14 results is warranted. For example, why is the DMSO signature in Figure 1 - supplement 4 so different from that of Figure 1?

In our previous study (Estevam et al., 2024), we more directly compared MET and METΔExon14, and while observed several differences, especially at conserved regulatory motifs, the TPR expression system did not provide a robust differential. Therefore, we hypothesize that a membrane-bound context is likely necessary to obtain a differential that captures juxtamembrane regulatory effects for these two isoforms. For that reason, we did not place heavy emphasis on the differences between MET and METΔExon14 in this study. Nevertheless, we performed parallel analysis of the METΔExon14 inhibitor DMS and provided all source and analyzed data in our GitHub repository (https://github.com/fraser-lab/MET_kinase_Inhibitor_DMS).

In our analysis of resistance, we used Rosace to score and compare DMSO and inhibitor landscapes. We present the full distribution of raw scores in Figure 1 for each condition. However, to visually highlight resistance mutations as a heatmap, we subtracted the scores of each variant in each inhibitor condition from the raw DMSO score, making the heatmaps in Figure 1 - supplement 4 appear more “blue.”

And finally, there is a lot of emphasis put on the unexpected results of this assay for the tivantinib "type III" inhibitor - could this in fact be because the molecule "is highly selective for the inactive or unphosphorylated form of c-Met" according to Eathiraj et al JBC 2011?

The work presented by Eathiraj et al JBC 2011 is a key study we reference and is foundational to tivantinib. While the point brought up about tivantinib’s selective preference for an inactive conformation is valid, this is also true for type II kinase inhibitors. In our study, regardless of inhibitor conformational preference, tivantinib was the only one with a nearly identical landscape to DMSO and exhibited selection even in the absence of Ba/F3 MET-addiction (Figure 1E). This result is in closer agreement with MET agnostic behavior reported by Basilico et al., 2013 and Katayama et al., 2013.

While this paper is crisply written with beautiful figures, the complexity of the data warrants a bit more clarity in how the results are visualized. Namely, clearly highlighting mutants that have previously reported and those identified by this study across all figures could help significantly in understanding the more novel findings of the work.

To better compare and contrast novel mutation identified in this study to others, we compiled a list of reported resistance mutations from recent clinical and experimental studies (Pecci et al 2024; Yao et al., 2023; Bahcall et al., 2022; Recondo et al., 2020; Rotow et al ., 2020; Fujino et al., 2019), since a direct database with resistance annotations does not exist for MET, to the best of our knowledge. In total, this amounted to 31 annotated resistance mutations across crizotinib, capmatinib, tepotinib, savolitinib, cabozantinib, merestinib, and glesatinib, which we have now tabulated in a new figure (Figure 4) and commentary in the main text:

To assess the agreement between our DMS and previously annotated resistance mutations, we compiled a list of reported resistance mutations from recent clinical and experimental studies (Pecci et al 2024; Yao et al., 2023; Bahcall et al., 2022; Recondo et al., 2020; Rotow et al ., 2020; Fujino et al., 2019) (Figure 4A,B). Overall, previously discovered mutations are strongly shifted to a GOF distribution for the drugs where resistance is reported from treatment or experiment; in contrast, the distribution is centered around neutral for those sites for other drugs not reported in the literature (Figure 4C). However, even in cases such as L1195V, we observe GOF DMS scores indicative of resistance to previously reported inhibitors. Given this overall strong concordance with prior literature and clinical results, we can also provide hypotheses to clarify the role of mutations that are observed in combination with others. For example, H1094Y is a reported driver mutation that has been linked to resistance in METΔEx14 for glesatinib with either the secondary L1195V mutation or in isolation (Recodo et al., 2020). However, in our assay H1094Y demonstrated slight sensitivity to gelesatinib, suggesting that either resistance is linked to the exon14 deletion isoform, the L1195V mutation, or a cellular factor not modeled well by the BaF3 system.

Finally, the potential impacts and follow-ups of this excellent study could be communicated better - it is recommended that they advertise better this paper as a resource for the community both as a dataset and as a proof of concept. In this realm I would encourage the authors to emphasize the multiple potential uses of this dataset by others to provide answers and insights on a variety of problems.

Please see below

Related to this, the decision to include the MetdelEx14 results, but not discuss them at all is interesting, do the authors expect future analyses to lead to useful insights? Is it surprising that trends are broadly the same to the data discussed?

Our previous paper suggests that Ba/F3 isn’t a great model for measuring the differences between MET and METΔEx14, so we haven’t emphasized other than to point to our previous paper. We include the full analysis here nonetheless as a resource. Potentially where the greatest differences between resistance mutant behaviors would be observed is in the full-length, membrane-bound MET and METΔEx14 receptor isoforms. While outside of the scope of this study, there is great potential to use the resistance mutations identified in this study as a filtered group to test and map differential inhibitor sensitivities between receptor isoforms.

And finally it could be valuable to have a small addition of introspection from the authors on how this approach could be altered and/or improved in the future to facilitate the general application of this approach for combination therapies for other targets.

See also reviewer 2 response where we have added text.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major points of revision:

(1) It seems like much of the structural interpretation of the inhibitor binding mode, outside of crizotinib binding, appears to come from docked models of the inhibitor to the MET kinase domain. Given the potential variability of the docked structure to the kinase domain, it would be useful for the authors to consider alternative possible binding modes that their docking pipeline may have suggested. It could also be useful to provide some degree of validation or contextualization of their docking models.

All individual figures are very carefully inspected based on either existing crystal structures of the inhibitor or closely related inhibitors (ATP, 3DKC; crizotinib, 2WGJ; tepotinib, 4R1V; tivantinib, 3RHK; AMG-458, 5T3Q; NVP-BVU972, 3QTI; merestinib, 4EEV; savolitinib, 6SDE). In total, four structural interpretations were the result of docking onto reference experimental structures (capmatinib, cabozantinib, glumetinib, glesatinib). As we wrote above, different conformations and binding modes are possible in predicted mutant structures (as we did here at scale) and included in the ML analysis already.

(2) In the first section, the authors classify an inhibitor as Type Ia on docking models, but mention the conflicting literature describing it as type Ib - it would be helpful to provide a contextualization of why this distinction between Ia and Ib matters, and what difference it might make. It would also be useful to know if their docking score only suggested poses compatible with Ia or if other poses were provided as well. Validation using other method might be beneficial, especially since they acknowledge the conflicting literature for classification. Or at least recontextualization that more evidence would be needed.

Kinase inhibitors have several canonical structural definitions we use to base the classifications in this study. Specifically, type I inhibitors are classified in MET by interactions with Y1230, D1228, K1110 in addition to its conformation in the ATP-binding site. Type I inhibitors are further subdivided into type 1a in MET if it leverages interactions with the solvent front and residue G1163. In prior literature referenced, tepotinib was classified as type 1b, which would imply it does not have solvent front interactions, like savolitinib (PDB 6SDE) or NVP-BVU972 (PDB 3QTI). However, in the tepotinib experimental structure (PDB 4R1V), we observed a greater structural resemblance to other type 1a inhibitors opposed to type 1b (Figure 1 - figure supplement 1b).

(3) The measure used to discuss resistance and sensitivity is ultimately a resistance score derived from the increase or decrease of the presence of a variant during cell growth. This is not a measure of direct binding. It would be helpful if the authors discussed alternative mechanisms through which these variants may impact resistance and/or sensitivity, such as stability, protonation effects, or kinase activity. The score itself may be convolving over all these potential mechanisms to drive GOF and LOF observed behavior.

See the response to the public review. Indeed, our ML framework explicitly included conformational and stability effects as significant in improving predictions.

(4) While it is promising to try and improve the predictive properties of ESM1b, it is not exactly clear why the authors considered their structural data of 11 inhibitors a sufficient dataset with which to augment the model. It would be useful for the authors to provide some additional context for why they wished to augment ESM1b in particular with their dataset, and provide any metrics indicating that their training data of 11 inhibitors provided an adequate statistical sample.

We don’t understand what this means. Sorry!

(5) The authors use ESM-1b to predict the fitness impact of each mutation and augment it using protein structural data of drug-target interactions. However, using an XGBoost regressor on a single set of 11 kinase-inhibitor interaction pairs is an incredibly sparse dataset to train upon. It would be useful for the authors to consider the limitations of their model, as well as its extensibility in the context of alternate binding poses, alternate conformations, or changes in protonation states of ligand or inhibitor.

On the contrary - this is 11 chemicals across 3000 mutations. We have discussed alternative interpretations above.

Minor points:

(1) It would also be useful for the authors to provide more context around their choice of regressor. XGBoost is a powerful regressor but can easily overfit high dimensional data when paired with language models such as ESM-1b. This would be particularly useful since some of the features to train on were also generated using existing models such as ThermoMPNN.

Yes - we are quite concerned about overfitting and have tried to assess overfitting by careful design of test and validation sets.

(2) The authors also mention excluding their DMSO and AMG458 scores in the model training and testing due to overfitting issues - it would be useful to have an SI figure pointing to this data.

No - we exclude the DMSO because that is the reference (baseline) and AMG because it has a different binding mode. This isn’t related to overfitting.

(3) The authors mention in their docking pipeline that 5 binding modes were used for each ligand docking, but it appears that only one binding mode is considered in the main figures. It would be useful for the authors to provide additional details about what were the other binding modes used for, how different were each binding mode, and how was the "primary" mode selected (and how much better was its score than the others).

The reviewer misinterprets the difference between poses shown in figures, based on mostly crystal structures or carefully selected templates, and the use of docked models in feature engineering for the ML part of the study. Where existing crystal structures do not exist, we performed docking for capmatinib, cabozantinib, glumetinib, glesatinib onto reference structures bound to type I (2WGJ) and type II (4EEV) inhibitors. We selected one representative binding mode based on the reference inhibitor, and while not exact, at a minimum these models provide a basis for structural interpretation.

Reviewer #2 (Recommendations for the authors):

My main suggestion is for the authors to add a few sentences (in non-technical language) to the results section, specifically before the results shown in Figure 3, defining gain-of-function, loss-of-function, resistance, and sensitivity. While these definitions are present in the materials and methods section, explicitly discussing them prior to the relevant results would significantly improve the overall readability of the manuscript.

We defined “gain-of-function” and “loss-of-function” mutations as those with fitness scores statistically greater or lower than wild-type. Within the DMSO condition, gain-of-function and loss-of -function labels describe mutational perturbation to protein function, whereas within inhibitor conditions, the labels describe the difference in fitness introduced by an inhibitor.

We have also clarified these definitions where the terms are first introduced: “As expected, the DMSO control population displayed a bimodal distribution with mutations exhibiting wild-type fitness centered around 0, with a wider distribution of mutations that exhibited loss- or gain-of-function effects, as defined by fitness scores with statistically significant lower or greater scores than wild-type, respectively.”

Figure 7D. Please add a bit more detail to the legend on how fold change (y-axis) was calculated.

Here, fold change represents the number of viable cells at each inhibitor concentration relative to the TKI control, measured with the CellTiter-Glo® Luminescent Cell Viability Assay (Promega) as an end point readout. We have updated the legend of Figure 7D with calculation details: “Dose-response for each inhibitor concentration is represented as the fraction of viable cells relative to the TKI free control.”

I must admit, I did not understand what "Specific inhibitor fitness landscapes also aid in identifying mutations with potential drug sensitivity, such as R1086 and C1091 in the MET P-loop" means. These are positions where most mutations lead to greater sensitivity to crizotinib. Is the idea that there are potentially clinically-relevant MET mutations that can be targeted over wild type with crizotinib?

Thank you for highlighting this! The P-loop (phosphate-binding loop) is a glycine-rich structural motif conserved in kinase domains. This motif is located in the N-lobe, where its primary role is to gate ATP entry into the active site and stabilize the phosphate groups of ATP when bound. Therefore, the P-loop is a common target region for ATP-competitive inhibitor design, but also a site where resistance can emerge (Roumiantsev et al., 2002). The idea we’d like to convey is that identifying residues that offer the potential for drug stabilization with the added benefit of having lower risk resistance, is an attractive consideration for novel inhibitor design.

We have added to the text: “Individual inhibitor resistance landscapes also aid in identifying target residues for novel drug design by providing insights into mutability and known resistance cases. This enables the selection of vectors for chemical elaboration with potential lower risk of resistance development. Sites with mutational profiles such as R1086 and C1091, located in the common drug target P-loop of MET, could be likely candidates for crizotinib.”

Reviewer #3 (Recommendations for the authors):

(1) Suggested Improvements to the Figures:

a)  Figure 4A - T1261 seems to be mislabeled

b)  In Figure 3A it's suggested to highlight mutants determined to be resistance mutants by this scheme.

c)  In Figure 3D it would be informative to highlight which of these resistance mutants have already been previously reported and which are novel to this study

d)  Throughout figures 3A, 3D, and 4G the graphical choices on how to highlight synonymous mutations and mutations not performed in the assay needs improvement.

The Green vs Grey 'TRUE' vs 'FALSE' boxes are confusing. Just a green box indicating synonymous mutations would be sufficient. Additionally these green boxes are hard to see, and often edges of this green box are currently missing making it even more difficult to see and interpret.

* In Figure 4A mutants do not seem to be indicated by a line or plus sign, but this is not explained in the legend or the caption. Please add.

* In 3D and 4G it is not clear if the mutants not performed are indicated at all - perhaps they are indicated in white, making them indistinguishable from scores with 0. Please clarify.

T1261 and G1242 are now correctly labeled.

In text we have also highlighted reported resistance mutations for crizotinib, which are inclusive of clinical reports and in vitro characterization: “These sites, and many of the individual mutations, have been noted in prior reports, such as: D1228N/H/V/Y, Y1230C/H/N/S, G1163R.”

We have adjusted the heatmaps to improve visual clarity. Mutations with score 0 are white, as indicated by the scale bar, and mutations uncaptured by the screen are now in light yellow. The green outline distinguishing WT synonymous mutations have also been adjusted so edges are no longer cut off. In our representations, we only distinguished mutations by the score color scale bar and WT outline. What looked like a “plus” or “line” in the original figure was only the heatmap background, which now should be resolved in the updated figure and legends for Figure 3 and Figure 4.

(2) Some Minor Suggested Improvements to the Text:

a)  The abbreviation CBL for 'CBL docking site' is used without being defined.

b)  Figure 3G is referenced, but it does not exist.

c)  In the sentence 'Beyond these well characterized sites, regions with sensitivity occurred throughout the kinase, primarily in loop-regions which have the greatest mutational tolerance in DMSO, but do not provide a growth advantage in the presence of an inhibitor (Figure 1 - Figure Supplement 1; Figure 1 - Figure Supplement 2).'. It is not clear why these supplemental figures are being referenced.

d)  In the supplement section 'Enrich2 Scoring' has what seem like placeholders for citations in [brackets]

Cbl is a E3 ubiquitin ligase that plays a role in MET regulation through engagement with exon 14, specifically at Y1003 when phosphorylated. This mode of regulation was more highlighted in our previous study. However, since Cbl was only mentioned briefly in this study, we have removed reference to it to simplify the text.

In addition, we have removed the figure 3G reference and corrected the in-text range. We have also removed references to figure supplements where unnecessary and edited the “Enrich2 scoring” method section to now reference missing citations.

Author response:

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

eLife Assessment

This is a useful report of a spatially-extended model to study the complex interactions between immune cells, fibroblasts, and cancer cells, providing insights into how fibroblast activation can influence tumor progression. The model opens up new possibilities for studying fibroblast-driven effects in diverse settings, which is crucial for understanding potential tumor microenvironment manipulations that could enhance immunotherapy efficacy. While the results presented are solid and follow logically from the model’s assumptions, some of these assumptions may require further validation, as they appear to oversimplify certain aspects in light of complex experimental findings, system geometry, and general principles of active matter research.

We thank the editor for recognizing the usefulness of our work. This work does not aim to precisely describe the complexity of the tumor microenvironment in lung cancer, but rather to classify and rigorously calibrate a minimum number of parameters to the clinical data we collect and generate, and reproduce the global structures of the microenvironment. We identify different scenarios, and show how they depend on the local interactions within this framework. Although we started in the first version with coalescence in the main text and anisotropic geometry in the supporting information, we realized that we needed to provide more directions to better show how our model can be extended. Thus, in Section III-4 we added an analysis of a microenvironment with blood vessels, and showed how to introduce anisotropic friction as a function of fiber orientation, as well as active stress, paving the way for further studies, that would make our model more complex. However, in a first step, it is crucial to start with a limited number of parameters that can be rigorously determined, and this is how this first work was conceived.

Public Reviews:

Reviewer #1 (Public review):

The authors present an important work where they model some of the complex interactions between immune cells, fibroblasts and cancer cells. The model takes into account the increased ECM production of cancer-associated fibroblasts. These fibres trap the cancer but also protect it from immune system cells. In this way, these fibroblasts’ actions both promote and hinder cancer growth. By exploring different scenarios, the authors can model different cancer fates depending on the parameters regulating cancer cells, immune system cells and fibroblasts. In this way, the model explores non-trivial scenarios. An important weakness of this study is that, though it is inspired by NSCLC tumors, it is restricted to modelling circular tumor lesions and does not explore the formation of ramified tumors, as in NSCLC. In this way, is only a general model and it is not clear how it can be adapted to simulate more realistic tumor morphologies.

We thank the reviewer for highligting the importance of our work. We acknowledge that although we provided anisotropic geometries and the study of the coalescence in the first version, more effort was needed to provide tools to extend our formalism to non-ideal cases. This is now added as Section III-4, where we analyze the impact of blood vessels, and the anisotropic friction due to the nematic order for the fibers; this nematic order can also be used to introduce active nematic stress.

Reviewer #2 (Public review):

Summary:

The authors develop a computational model (and a simplified version thereof) to treat an extremely important issue regarding tumor growth. Specifically, it has been argued that fibroblasts have the ability to support tumor growth by creating physical conditions in the tumor microenvironment that prevent the relevant immune cells from entering into contact with, and ultimately killing, the cancer cells. This inhibition is referred to as immune exclusion. The computational approach follows standard procedures in the formulation of models for mixtures of different material species, adapted to the problem at hand by making a variety of assumptions as to the activity of different types of fibroblasts, namely ”normal” versus ”cancer-associated”. The model itself is relatively complex, but the authors do a convincing job of analyzing possible behaviors and attempting to relate these to experimental observations.

Strengths:

As mentioned, the authors do an excellent job of analyzing the behavior of their model both in its full form (which includes spatial variation of the concentrations of the different cellular species) and in its simplified mean field form. The model itself is formulated based on established physical principles, although the extent to which some of these principles apply to active biological systems is not clear (see Weaknesses). The results of the model do offer some significant insights into the critical factors which determine how fibroblasts might affect tumor growth; these insights could lead to new experimental ways of unraveling these complex sets of issues and enhancing immunotherapy.

We thank the referee for this summary and for recognizing the strengths of our paper.

Weaknesses:

Models of the form being studied here rely on a large number of assumptions regarding cellular behavior. Some of these seemed questionable, based on what we have learned about active systems. The problem of T cell infiltration as well as the patterning of the extracellular matrix (ECM) by fibroblasts necessarily involve understanding cell motion and cell interactions due e.g. to cell signaling. Adopting an approach based purely on physical systems driven by free energies alone does not consider the special role that active processes can play, both in motility itself and in the type of self-organization that can occur due to these cell-cell interactions. This to me is the primary weakness of this paper.

We thank the referee for this important comment, that allows us to clarify this important point. Although biological materials are out of equilibrium, their behavior often resembles that dictated by thermodynamics. Hence the usefulness of constructing a free energy, in terms of these variables. In a first approach to decipher the complex interactions and describe the different and sometimes non-trivial outcomes in this system that involves many components, we must start by minimizing the number of parameters, and identifying those complex processes, that control the evolution of the system. The free energy that we build on this biological system contains therefore out-of-equilibrium processes that can be approximated by a ”close to equilibrium” description. Our approach is a classical one in statistical physics of active systems, namely in the effort to construct an equivalent free-energy for out-of-equilibrium systems. This allows to gain a clearer insight into those complex processes.

We have added a sentence in the main text, section III.1, to clarify this point:

“Building a free-energy density for a biological material is justified, because, although biological materials are out of equilibrium, their behavior often resembles that dictated by thermodynamics. It is therefore useful to write a free energy in terms of state variables.”

Nevertheless, we recognize that we should have provided more tools for using our formalism by making it active. This is why we introduced the nematic order in the fibers in Section III-4. This nematic order can be used to introduce active stress, and we have cited previous works by some of us see [?, ?, ?] as references for building active processes out of it.

We must also note that cell signaling has been introduced a minima in our system for providing the cue for the arrival of T-cells and NAFs from the boundaries. However, we found that although we had evoked the other role of the chemicals in the transformation from NAFs to CAFs in the text, details were not well explained. We have therefore corrected and added some explanations in the introduction of section III, and III.1, III.2.

A separate weakness concerns the assumption that fibroblasts affect T cell behavior primarily by just making a more dense ECM. There are a number of papers in the cancer literature (see, for some examples, Carstens, J., Correa de Sampaio, P., Yang, D. et al. Spatial computation of intratumoral T cells correlates with survival of patients with pancreatic cancer. Nat Commun 8, 15095 (2017);Sun, Xiujie, Bogang Wu, Huai-Chin Chiang, Hui Deng, Xiaowen Zhang, Wei Xiong, Junquan Liu et al. ” Tumour DDR1 promotes collagen fibre alignment to instigate immune exclusion.” Nature 599, no. 7886 (2021): 673-678) that seem to indicate that density alone is not a sufficient indicator of T cell behavior. Instead, the organization of the ECM (for example, its anisotropy) could be playing a much more essential role than is given credit for here. This possibility is hinted at in the Discussion section but deserves much more emphasis.

The referee is right in his comment, and we thank him for raising this issue. We have therefore introduced the anisotropic orientation of the fibers, which induces an anisotropic friction in a new section III-4. In addition, the references pointed out were included in this section. However, although the anisotropy strongly influences the fate of the tumor when the fibers are oriented perpendicular to the surface of the cancer nest, it is less effective when the fibroblasts are oriented in the direction of surface of the cancer nest. In the latter case, which is often the case before cancer cells reshape the tumor microenvironment, the matrix density should correlate with the friction.

Finally, the mixed version of the model is, from a general perspective, not very different from many other published models treating the ecology of the tumor microenvironment (for a survey, see Arabameri A, Asemani D, Hadjati J (2018), A structural methodology for modeling immune-tumor interactions including pro-and anti-tumor factors for clinical applications. Math Biosci 304:48-61). There are even papers in this literature that specifically investigate effects due to allowing cancer cells to instigate changes in other cells from being tumor-inhibiting to tumor-promoting. This feature occurs not only for fibroblasts but also for example for macrophages which can change their polarization from M1 to M2. There needed to be some more detailed comparison with this existing literature.

The referee is right that the first part of our approach, namely the dynamical system may be common in this kind of system, and it needs to be mentioned. So we added the following sentence in the discussion: ”This is in line with several similar mathematical models, that study through this lens the inhibition/activation of the immune system by cancer cells either by means of compartmental nonlinear models similar to our dynamical system, for instance regarding macrophage recruitment and cytokine signaling {arabameri2018structural} {li2019computational}, or mixture models {fotso2024mixture}. We combine the two approaches in order to rigorosly derive the parameters of the model and gain insights from both.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors should address the following points:

Major issues

(1) The shape of tumors simulated differs immensely from the observed tumors in Fig. 2. Here, the tumor is constituted by irregular domains, not dissimilar from domains in phase separating mixtures. The domains simulated are circular. Since the authors are using the space dependent model to model the increase in tumor cells with time in the different scenarios (immune-desert, immune-excluded, immune inflamed), it should explain how non-spherical tumor structures can be observed in these scenarios. The authors introduce tumor coalescence in page 28, however, it is not expected that the structures observed in Fig 2 are the result from different tumors merging and coalescing, because that would result from an unlikely large number of initial mutation events in the same region of the tissue. The authors should explain what mechanisms present in the model can lead to non-spherical forms.

We agree with the reviewer that real tumors are rarely round contrary to what our numerics suggests. In fact, only the last figure of our paper in the supporting information was more appropriate for such a discussion. We are now adding discussions and new figures to better illustrate our spatial model, see Figure 6 and section III-4. The in situ geometry of tumors depends on the shape of the host organ, the diffusive (chemical) or advected species such as T cells and fibroblasts, and on the nutrients. Thus, in our case, only cancer cells are produced locally, but during growth the tumor is strongly constrained by the microenvironment, and thus the geometry of the domain we model in the numerics and its boundary conditions. This is also true for the chemicals responsible for growth, cellular advection and phenotypic transformation. Their concentration depends on a convection-diffusion equation and boundary conditions. For a tumor in situ, such as in the lung, the available space is a constraint that will dominate the final geometry of the tumor nests. We do not think that coalescence is controlled by mutational events, but most likely by the search for space necessary for growth. Compared to the first version, we add new figures (Figure 6) that show that the geometry of the organ, as well as the localization of blood vessels, are a cause of the irregularity of the tumor shapes. We also introduce orientational order, which as suggested in section III-4, can induce anisotropic friction and stresses, as well as anisotropic growth. We cite (Ackermann, Joseph, and Martine Ben Amar. ”Onsager’s variational principle in proliferating biological tissues, in the presence of activity and anisotropy.” The European Physical Journal Plus 138.12 (2023): 1103.) where we described active stresses and coupling related to anisotropic growth.

(2) According to the authors, the model presented in equations (1) and onwards simulates the evolution of the fraction of tumor cells in the tissue. However the fraction of tumor cells, for example, depends itself on the variation of other cell types. For example, if fibroblasts were to proliferate with rate alpha, even without tumor cells proliferating, the fraction of tumor cells in the mixture should decrease as alpha times the tumor cells fraction. These terms are missing. The equations do not describe the evolution of the cells’ fractions but of the amount of cells of each type, normalised by the total carrying capacity of non-normal cells in the tissue. The text should be rewritten accordingly.

We agree with the referee: our definition of cell density was not precise enough and may appear misleading. In the paragraph II1, we more explictly introduce the word mass fraction which is the correct physical quantity to introduce into the spatial model.

”All these cells have the same mass density and the sum of their mass fraction satisfies the relationship S = C + T + F_NA + F_A = 1-N, where N is a healthy non active component as healthy cells, for example.”

It is less intuitive than ”number of cells per unit volume” but necessary for the following (III)

(3) The authors start by calculating fixed points of different versions of the dynamical system without spatial dependence. They should explain what is the relevance of these fixed points: in a real situation, where the concentration of tumor fibroblasts and T-cells depend on position, in which conditions are these fixed points relevant?

The referee is right and we will clarify this point: the dynamic analysis is a help for understanding and predicting the scenario occurring in the system. After all the steps of paragraph 2.2, we are faced with 11 independent parameters only for the dynamical system and without the parameters generated by the space modeling itself. Our estimation concerns only lung cancer. These parameters do not appear in the literature. The parameters introduced in Sec. III which are more related to physical interactions such as friction, cell-cell adhesion, etc. can be found in the literature or can be estimated and thus measured in in vitro experiments (see Ackermann and Ben Amar, EPJP 2023, P. Benaroch, J. Nikolic et al. 2024, biorxiv). So what are the fixed points for: they help to get the right numbers for spatial analysis. To recover special features of cancer evolution, we need a model, but also correct estimates of the data in a code that is quite technical and heavy, with each simulation taking a certain amount of time. For users who only need rough predictions, the analysis in section 2 is sufficient.

It is also important to note that the global result depends only on the source terms, and on the boundary conditions. This can be illustrated with a simple example: Consider the governing equation for the density of a component with velocity v and source term:

Integrating the equation over a fixed volume V of surface S gives:

. This integrated equation can then be approximated by the dynamical system that we write. Thus, while the dynamical system does not give any information about the local structure of the system, it may be indicative of its global outcome.

(4)   In page 15, the authors identify that α_NA is proportional to δ𝝐⁴. However, in equation (7), they replace α_NA by δ𝝐⁴ without the proportionality constant. This should be corrected.

Thank you for your remark. This typo is now corrected.

(5) The tumor cell movement should be much slower than the T-cells. Here, the authors assign a similar friction coefficient for the cancer cells and T-cells, for example. However, in lung cancer tumor cells are epithelial, and adhere to each other in the tissue. Their movement is very restricted by the basement membranes and by cell-cell adhesion. Immune cells and T-cells on the other hand move rapidly throughout the stroma. It is a gross simplification to not consider the low epitelial tissue mobility in the context of lung cancer.

It is possible to assume different friction coe cients for each phase pair. This has been done in a previous publication, Ackermann et al., Physics report 2021. It is also possible to play with the cell-cell adhesion in the energy density and on the diffusion coe cient introduced in the Flory-Higgins free energy. Cell-cell adhesion is taken into account in the energy, and this makes the tumor a more dense phase, while T-cells can move towards cancer cells to which they are attracted. In the last part of the paper, we show the role of an anisotropic friction due to a nematic order for activated fibroblasts and all the other cells

(6) What is the biological mechanism by which the T-cells form a colony with a surface tension? In the phase-field model, the authors have a surface tension assigned to the cancer cells, T-cells and fibroblasts. Can the authors justify biologically why do they consider these surface tensions?

The fact that T-cells form a colony is due to the accumulation of T-cells at the outer boundary of the tumor, as they are attracted to it but cannot penetrate due to the strong cell-cell adhesion of the tumor cells in the nest. Adding a gradient square is standard in continuous models to limit the sharp variations. In a continuous approach, the gradient square contribution limits the sharp variations in cell density which are not physical.

Minor issues

(a) Page 6 (end), characterisation of the fibre barrier produced by CAFs missing: what is the fibre density, how it can hinder the spread of cancer and T-cell motility? Is it so dense that it prevents ameboid movement? Can cells move through it using matrix degradation proteins?

The fiber density corresponds to the fibrous organic extracellular matrix secreted by cancer-associated fibroblasts. In desmotic (highly fibrous tumors such as PDAC or NSCLC), this extracellular matrix deposited around the tumor forms a physical barrier around the tumor nest, preventing both cell migration and capillary and immune cells penetration. In these cases, the fibrous belt actually prevents ameboid movement and cells must deform significantly to migrate. The role of this barrier was particularly demonstrated in the reference (Grout, John A., et al. ”Spatial positioning and matrix programs of cancer-associated fibroblasts promote T-cell exclusion in human lung tumors.” Cancer Discovery 12.11 (2022): 2606-2625.). In later stages of cancer, the tumor may adapt and develop strategies to metastasize, such as matrix degradation. This matrix can be oriented, organized or disordered. To build a minimal model, we first considered an isotropic friction and also an anisotropic friction of the nematic belt, due to the activated fibroblasts. In the case of T-cells, as mentioned in section I.1, it is true that the biological literature also considers a phenotypic transformation of the T cells by the activated fibroblasts: this concerns both their proliferative capacities, antigen recognition and also their cytotoxic function. To better document the different mechanisms, we add the following publication: Cancer associated fibroblasts-an impediment to effective anti-cancer T cell immunity, by Koppensteiner, Lilian and Mathieson, Layla and O’Connor, Richard A and Akram, Ahsan R, Frontiers in immunology (2022).

However, our goal is to build a minimal model and to characterize and quantify the physical process in which CAFs are involved, namely the role of a physical barrier, that has been documented, as documented above.

(b) Page 19 (Fig 3), in the figure legend it is written ”resting fibroblasts”, should be ”non-activated fibroblasts”.

The referee is right: it will be better to write non-activated fibroblasts. This is now changed in the main text.

(c) Page 21 (equation), what is dΩ? It is dr?

We thank the referee for raising this point. The text was indeed ambiguous as sometimes dΩ was replaced by dr. To be clearer, all the elements of volume are now noted dV , and the element of surface of the system are noted dS.

In the article the units are in italic and should be in roman.

Thank you for raising this point. It has been corrected.

(d) Page 25 (beginning section III.3), the authors mention that the simulation is 2D, however, the simulation has radial symmetry. A 1D simulation in radial coordinates could simulate a 3D spherical system. Is the simulation of this section equivalent to a 1D radial simulation (in 2D)?

The referee is right that in radial symmetry, a 1d equation may be written. We therefore present numerics with irregular shapes of the tumor nest in order to make the system fully 2d.

(e) Page 26 (Fig 4). Legends inside the plots of plates A, B, C and D are not clear. Colorbar range of plates A and D is different. Would facilitate if the ranges were the same.

The referee is right: the surface plots presented in figure 4 would be easier to compare with the same colorbar range for the legends. In fact, as the referee noted, figures in A, B and C have the same legends, while figure in D has a different one. This is due to the fact that D represents the case of the immune-inflamed tumor where the cancer mass fraction is quite vanishing, resulting in values that are of 3 orders of magnitude lower than those present in A, B and C. Therefore, they would disappear if the colorbar range were equal to the others.We insist more on the change of scale in the legend of Figure 4, in the new version.

(f) Page 29 (Fig 5), would facilitate if the order of immune-desert, immune-excluded, immune-inflamed was maintained throughout the document. In this figure the immune-inflamed case appears first.

We agree with the reviewer that following the same order in which the different cases are presented throughout the manuscript would be helpful in comparing the different figures. Therefore, we have modified Figure 5.

(g) Page 31, the authors indicate that pharmacodynamics and pharmacokinetics are highly dependent on tumour spatial structure. Can they provide examples and citations?

In the discussion, we have added references concerning pharmacodynamics.

(h) Page 33 (Fig Sup2), would facilitate if the order of immune-desert, immune-excluded, immune-inflamed was maintained throughout the document. ±±

We thank the reviewer for pointing this out, the order of the different scenarios in Fig Sup 2 has now been changed.

Reviewer #2 (Recommendations for the authors):

Major points

(1) Following on from the discussion in the public review, I feel that there are a number of critical issues that need to be addressed regarding modeling assumptions. I would like to understand why the authors believe it is possible to use a free energy-driven model of the microenvironment when many of the processes relevant for their study have an undeniably ”active media” flavor.

The referee is right that processes in biology are active processes. However, it is a classical approach to model physical interactions between biological components with a free-energy, especially cell adhesion, as they often lead to quasi-stationary equilibrium-like patterns. The free-energy approach has also the advantage to derive straight-forwardly complex phenomena involving many components. Activity can indeed be introduced in such a framework, if we know that the fibroblasts transform into myo-fibroblasts, see for example our previous publication Ackermann and Ben Amar, EPJP 2023. However, in the interest of simplification and reduction of the number of free parameters, we have not not considered further complication of the model here, as a minimal model allows to distinguish the main processes that occur. Nevertheless, introducing more precisely activity, in the nematic approach already achieved for the friction, is a natural continuation of our work: See the new Section III-4, where we introduce the nematic order, and we indicate that active nematic stresses can be written from it.

Next, I don’t understand the assumption that T cells do not proliferate once they detect neoantigens on the cancer cells; activation of T cells usually causes them to become more proliferative.

We thank the referee for this question. The T-cell fraction has two origins: proliferation of T-cells in situ in the stroma or inside tumor nest or external arrival from the sources that we privilege. We recognize that a full analysis of the tumor-microenvironment would require to consider proliferation near the tumor, as many more other processes which is do able but requires the knowledge of more biological date. In addition, besides, the proliferation of T-cells will be equivalent to increase the killing abilities of T-cells and these two effect overlapp in our approach.

In order to clarify this point, we modify the following sentence in Section II.2:

“Although proliferation of cytotoxic T-cells has been observed, we do not consider explicitly proliferation in our study as we focus on their ability to infiltrate the tumor.”

Rather, we consider that T-cells proliferate outside the domain boundaries, so that this proliferation is included in the boundary source contributions.

Finally, the issue of whether the density of fibers is sufficient to understand the role of fibroblasts is not at all settled. There should be a full discussion of this issue including mentioning of the Nature paper (cited in the public review) that argues that orientation (and not density) is the key to the role of fibers, as well as the earlier cited work of Kalluri and collaborators on the role of ECM density in pancreatic cancer.

We thank the referee for this remark. As we wrote above in the response to the public review, we introduced significant additions that aim to tackle this question in the article.

(2) The authors present a picture of a tumor cell with fibroblasts apparently arrayed circumferentially around the tumor boundary and therefore blocking infiltration. This type of tumor structure has been seen before, for example in ”On the mechanism of long-range orientational order of fibroblasts.” Proceedings of the National Academy of Sciences 114, no. 34 (2017): 8974-8979, which should be cited. More importantly, in that paper the argument is made that positive feedback between fibroblasts and ECM geometry can cause structures like this to form. If this is indeed what is occurring, this would indicate the crucial importance of a mechanism beyond what is contained in the current model. This issue should therefore be discussed within this paper. This issue is of course connected to the previous point regarding the role of ECM structure beyond density.

We completely agree that the interplay between the fibroblast layer and the tumor shapes the tumor boundary. One of the authors has worked recently on this precise topic (Aging and freezing of active nematic dynamics of cancer-associated fibroblasts by fibronectin matrix remodeling, C Jacques, J Ackermann, S Bell, C Hallopeau, CP Gonzalez, ... bioRxiv, 2023.11. 22.568216, Ordering, spontaneous flows and aging in active fluids depositing tracks S Bell, J Ackermann, A Maitra, R Voituriez arXiv preprint arXiv:2409.05195). Since the fibroblast layer is an active material, it contributes to an anisotropic stress that can be introduced into the model. Our first strategy was to present the simplest modeling in order to focus on the most important interactions as cell-cell adhesion and cell-tissue adhesion. However, we recognize that those questions should be discussed in the text, and we discuss it in the new section III-4

Minor points

There are also a number of more minor points to consider:

(1) Since the parameter is taken to be O(1), why exactly does it matter how the other parameters scale with it?

It is very important to compare the order of magnitude of the other parameters once the selected parameter of order O(1) is really the driving parameter of the coupling. It gives a first picture of the main interactions that has to consider.

(2) I didn’t understand the relevance of referring specifically to IL 6 among many other possibly relevant signals, as is currently done on page 7.

This corresponds to studies aiming to correlate lung cancer risks and the concentration of interleukin, mostly IL6 and IL8 (McKeown, D. J., et al. ”The relationship between circulating concentrations of C-reactive protein, inflammatory cytokines and cytokine receptors in patients with non-small-cell lung cancer.” British journal of cancer 91.12 (2004): 1993-1995.,Brenner, Darren R., et al. ”Inflammatory cytokines and lung cancer risk in 3 prospective studies.” American journal of epidemiology 185.2 (2017): 86-95. ) but in the absence of very detailed biological information, the modeling and its results are not modified if other chemicals intervene..We slightly modeified the following phrase in section I.1:

“In particular, in the family of inflammatory proteins, also called cytokines, Interlukin-6 (IL6) and (IL8) seem, among others to stimulate the infiltration of CD8⁺.

(3) The authors need to mention the possibility of T-cell chemotaxis to the tumor being ”self-amplified” in the T cell system, as put forth in Galeano Nin˜o, Jorge Luis, Sophie V. Pageon, Szun S. Tay, Feyza Colakoglu, Daryan Kempe, Jack Hywood, Jessica K. Mazalo et al. ”Cytotoxic T cells swarm by homotypic chemokine signalling.” eLife 9 (2020): e56554. This might again reveal a needed extension of the current modelling strategy.

We thank the referee for his/her comment on the self-amplification of T-cell population in the stroma and we mention the indicated reference in our paper. This auto-chemoatactic process which induces a dynamic of more e cient recruitment towards the tumor, may be important for immunotherapy. To have more e cient T-cell arriving at the site of the tumor, will lead a better issue for the patient, if the swarming organization is maintained in a desmoplastic nematic stroma.

(4) It is not obvious to me that in sub figures 3F and 3H the tumor is enroute to being totally eradicated, as is stated in the text. The blue lines seemed to asymptote at non-zero population values.

Looking at sub-figures 3F and 3H, we stated in the main text that the tumor is eradicated as the representative population approaches a 0 value fraction, or at least decays around the 0 (0.01/0.05 to be more precise). This is even more evident when compared with the other cases where the tumor mass fraction reaches values of a higher order (up to 0.6), thus leading us to dinstinguish between these different scenarios.

(5) The description of the interaction of cells with fibers as being increased friction might be misleading, as the real effect could be actual trapping in the network (as opposed to just slowing down the motion).

We thank the referee for this question as it allow us to make an important distinction. Indeed, what the referee describes seems to correspond to a discrete event, namely a cell trapped in a network. However, coarse-graining the dynamics to the continuous modeling seems to us as leading to an effective friction between the two phases. Moreover, we also now introduced an anisotropic friction which can represent a trapping. The velocities are not only directed around the tumor but can also be oriented towards the tumor, so that eventually the friction along the radius mimics a trapping (see Fig.4 on top). We have introduced this anisotropic friction via a nematic model, see the appendix.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary: 

In organisms with open mitosis, nuclear envelope breakdown at mitotic entry and re‐assembly of the nuclear envelope at the end of mitosis are important, highly regulated processes. One key regulator of nuclear envelope re‐assembly is the BAF (Barrier‐to‐Autointegration) protein, which contributes to cross‐linking of chromosomes to the nuclear envelope. Crucially, BAF has to be in a dephosphorylated form to carry out this function, and PP2A has been shown to be the phosphatase that dephosphorylates BAF. The Ankle2/LEM4 protein has previously been identified as an important regulator of PP2A in the dephosphorylation of BAF but its precise function is not fully understood, and Li and colleagues set out to investigate the function of Ankle2/LEM4 in both Drosophila flies and Drosophila cell lines.

Strengths: 

The authors use a combination of biochemical and imaging techniques to understand the biology of Ankle2/LEM4. On the whole, the experiments are well conducted and the results look convincing. A particular strength of this manuscript is that the authors are able to study both cellular phenotypes and organismal effects of their mutants by studying both Drosophila D‐mel cells and whole flies.

The work presented in this manuscript significantly enhances our understanding of how Ankle2/LEM4 supports BAF dephosphorylation at the end of mitosis. Particularly interesting is the finding that Ankle2/LEM4 appears to be a bona fide PP2A regulatory protein in Drosophila, as well as the localisation of Ankle2/LEM4 and how this is influenced by the interaction between Ankle2 and the ER protein Vap33. It would be interesting to see, though, whether these insights are conserved in mammalian cells, e.g. does mammalian Vap33 also interact with LEM4? Is LEM4 also a part of the PP2A holoenzyme complex in mammalian cells? 

We feel that conducting experiments to test the level of conservation of our findings in mammalian cells is outside the scope of our study, and we will leave it for other labs to investigate.

Weaknesses: 

This work is certainly impactful but more discussion and comparison of the Drosophila versus mammalian cell system would be helpful. Also, to attract the largest possible readership, the Ankle2 protein should be referred to as Ankle2/LEM4 throughout the paper to make it clear that this is the same molecule. 

We have reinforced our presentation and discussion of similarities and differences between Ankle2 from Drosophila vs humans where relevant throughout the Introduction and Discussion sections. Additionally, we have added the mention that Ankle2 is also called LEM4 in humans in the Abstract and Introduction. However, when referring to Drosophila Ankle2, we do not use LEM4 because it is not listed as an alternate name for this gene/protein in FlyBase.

A schematic model at the end of the final figure would be very useful to summarise the findings.

We have already provided a schematic model in Figure S3, where we think it is better placed.

Reviewer #2 (Public review):

The authors first identify Ankle2 as a regulatory subunit and direct interactor of PP2A, showing they interact both in vitro and in vivo to promote BAF dephosphorylation. The Ankyrin domain of Ankle2 is important for the interaction with PP2A. They then show Ankle2 also interacts with the ER protein Vap33 through FFAT motifs and they particularly co‐localize during mitosis. The recruitment of Ankle2 to Vap33 is essential to ER and nuclear envelop membrane in telophase while earlier in mitosis, it relies on the C terminus but not the FFAT motifs for recruitments to the nuclear membrane and spindle envelop in early mitosis. The molecular determinants and receptors are currently not known. The authors check the function of the PP2A recruitment to Ankle2/Vap33 in the context of embryos and show this recruitment pathway is functionally important. While the Ankle2/Vap33 interaction is dispensable in adult flies ‐looking at wing development, the PP2A/Ankle2 interaction is essential for correct wing and fly development. Overall, this is a very complete paper that reveals the molecular mechanism of PP2A recruitment to Ankle2 and studies both the cellular and the physiological effect of this interaction in the context of fly development.

Strengths: 

The paper is well written and the narrative is well‐developed. The figures are of high quality, wellcontrolled, clearly labelled, and easy to understand. They support the claims made by the authors. 

Weaknesses: 

The study would benefit from being discussed in the context of what is already known on Ankle2 biology in C.elegans and human cells. It is important to highlight the structures shown in the paper are alphafold models, rather than validated structures. 

We have enhanced our presentation of what is known about LEM‐4L/Ankle2 in C. elegans and humans in the Introduction, and further developed comparisons of our findings regarding Drosophila Ankle2 with these orthologs in the Results and Discussion sections. We have also specified in all sections and figure legends that the structures shown are AlphaFold3 models.

Reviewer #3 (Public review): 

Summary: 

The authors were interested in how Ankle2 regulates nuclear envelope reformation after cell division. Other published manuscripts, including those from the authors, show without a doubt that Ankle2 plays a role in this critical process. However, the mechanism by which Ankle2 functions was unclear. Previous work using worms and humans (Asencio et al., 2012) established that human ANKLE2 could bind endogenous PP2A subunits. The binding was direct and was mediated through a region before and including the first ankyrin repeat in human ANKLE2. In addition to its interaction with PP2A, Asencio et al., 2012 also show that ANKLE2 regulates VRK1 kinase activity. Together PP2A and VRK1 regulate BAF phosphorylation for proper nuclear envelope reformation. Here, the authors provide more evidence for interaction with PP2A by also mapping the domain of interaction to the ankyrin repeat in Drosophila. In addition, the ankyrin repeat is essential for nuclear envelope reformation after division. They show that Ankle2 can bind in a PP2A complex without other known regulatory subunits of PP2A. The authors also identify a novel interaction with ER protein Vap33, but functional relevance for this interaction in nuclear envelope reformation is not provided in the manuscript, which the authors explicitly state. This manuscript does not comment on the activity of Ballchen/VRK1 in relation to Ankle2 loss and BAF phosphorylation or nuclear envelope reformation, even though links were previously shown by multiple studies (Asencio et al., Link et al., Apridita Sebastian et al.,). Nuclear envelope defects were rescued by the reduction of VRK1 in two of these manuscripts. It is possible that BAF phosphorylation phenotypes can be contributed by both PP2A inactivity and VRK1 overactivity due to the loss of Ankle2.

Strengths: 

This manuscript is a useful finding linking Ankle2 function during nuclear envelope reformation to the PP2A complex. The authors present solid data showing that Ankle2 can form a complex with PP2A‐29B and Mts and generate a phosphoproteomic resource that is fundamentally important to understanding Ankle2 biology. 

Weaknesses: 

However, the main findings/conclusions about subcellular localization might be incomplete since they are drawn from overexpression experiments. In addition, throughout the text, some conclusions are overstated or are not supported by data. 

It is true that all experiments studying subcellular localization were done with tagged proteins overexpressed in flies and cell culture. Nevertheless, we show that Ankle2‐GFP is functional since it rescues phenotypes resulting from the loss of endogenous Ankle2 in both flies and cultured cells. The antibodies we generated against Ankle2 were unable to reliably detect the endogenous protein by immunofluorescence. We have now stated this caveat in our manuscript. Regarding the validity of our conclusions in relation to our data, we address each point raised by the reviewer under the Recommendations for the authors. In some cases, we have adjusted our conclusions and in other cases, we have provided additional clarification or justification. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

There are a few experimental issues that should be addressed, specific comments are listed below: 

(1) Figure 1F: In this experiment, the authors immunoprecipitate GFP‐PP2A‐29B or PP2A‐B29BGFP and Western blot for Ankle2 and Mts to demonstrate that both are co‐immunoprecipitated. To demonstrate that these interactions are specific, the authors should also blot for a protein that is expected to definitely NOT co‐immunoprecipitate with PP2A‐B29; e.g. tubulin. 

Our conclusion that GFP‐PP2A‐29B and PP2A‐29B‐GFP specifically interact with Ankle2 and Mts is also based on mass spectrometry analysis of the purification products from embryos and cells in culture, comparing with products of purification of GFP alone (Fig 1E‐F, S1C‐D and Tables S2, S3). The lists of identified proteins reveal that most proteins (including tubulins) are not enriched with GFP‐PP2A‐29B or PP2A‐29B‐GFP like Ankle2 and Mts are.

(2) Figure 2A: The colour coding of the dots is not explained in the figure legend. 

We have now added the explanation.

(3) Figure 2B: The competition experiment is a good idea. Do the authors get the same results when they conduct the experiment the other way round, i.e. keep the concentration of Tws the same but increase the concentration of Ankle2? 

We have tried this reverse experiment but saw little effect. The failure to observe displacement of Tws by Ankle2 in this context could be due to a higher affinity of Tws than Ankle2 in the PP2A complex, or to lower expression levels achieved for Ankle2 (a larger protein) relative to Tws.

(4) Figure 5D: The hyperphosphorylation of BAF is very difficult to see, and it is impossible to tell whether the hyperphosphorylation has been rescued or not by the different Ankle2 constructs. Can the phosphorylated and the hyperphosphorylated bands be separated better? This panel needs significant improvements to support the claims in the text.

In our opinion, the hyperphosphorylated (upper band) and unphosphorylated (lower band) forms of BAF are well resolved and readily distinguishable. The fainter band in the middle could correspond to a partially phosphorylated form of BAF but we do not venture to speculate on its precise identity nor do we need it to draw our conclusions. The important information from this blot is that the level of unphosphorylated BAF after Ankle2 RNAi increases when Ankle2WT‐GFP and Ankle2Fm+FL1‐GFP are expressed but not when Flag‐GFP or Ankle2ANK‐GFP are expressed. In these experiments, the rescue of unphosphorylated BAF is incomplete because not all cells express the GFP‐tagged protein in our non‐clonal stable cell lines.

Reviewer #2 (Recommendations for the authors):

(1) The alphafold models need to be labelled as such better on the figures, to distinguish them from X‐ray crystallography structures. Alphafold will always propose a solution but it is not necessarily correct. 

We have added the note “MODEL” directly in Figures 2C, 2D, 4F and S3B, in addition to the information already provided in the text and figure legends specifying that these are models generated by AlphaFold3.

(2) Figure 4 F. Annotate the Ankle2 FL1 peptide. 

We have indicated the amino acid residues in the figure.

(3) Problems with the statistical tests. T‐tests cannot be used for comparing multiple groups, as this favors error propagation. 

All of our t‐tests compare only two groups at a time, as indicated. In this regard, our labeling in Fig 5C may have been misleading. We have now changed it.

(4) Close‐ups of ring canal in Figure S2. In Figure S2, there seem to be lots of GFP‐Ankle2 vesicles in the cytoplasm of the oocyte. 

We agree that the image showing Ankle2‐GFP alone in the RNAi Vap33 condition suggested a cytoplasmic granular localization of unknown nature. However, upon examination, we realized that this image did not correspond to the same z‐step as the matching merged image (which also

included DNA staining). We have now replaced the image with the correct one.

Reviewer #3 (Recommendations for the authors): 

Be more accurate about what conclusions can be made from reported data, particularly from overexpression and deletion studies. 

(1) The domain analysis for physical interaction is quite thorough. However, localization information is taken from overexpressed constructs. While these data show what could happen, the authors are not using endogenous levels of Ankle2 in cells or tissues that are known to require Ankle2. As a result, it is difficult to determine whether localization results are biologically meaningful. 

We have added the following text at the end of the third Results section:

“We were unable to examine the localization of endogenous Ankle2 because the antibodies that we generated gave inconclusive results in immunofluorescence. For the remainder of our study, we relied on the overexpression of Ankle2‐GFP, which may not perfectly reflect the localization and function of endogenous Ankle2. However, Ankle2‐GFP is functional as it can rescue phenotypes observed when endogenous Ankle2 is depleted (see below).”

(2) The data showing that Ankle2 is a regulator unit of the PP2A complex also relies on in vitro binding assays in an over‐expression context. Data certainly show Ankle2 can bind proteins in the PP2A complex when overexpressed. However, the authors could not isolate enough of the complex from the animal to test function, so Ankle2 acting as a regulatory subunit isn't functionally shown. There are other possibilities, such as Ankle2 acts as a scaffold for complex assembly.  

The competition experiments shown in Fig 2 are based on complexes assembling in cells and are not in vitro binding assays. We show 4 lines of evidence supporting the idea that Ankle2 functions as a regulatory subunit of PP2A: 1) Ankle2 interacts with the structural (PP2A‐29B) and catalytic (Mts) subunits of PP2A without any known regulatory subunit of PP2A. 2) Depletion of Ankle2 leads to the hyperphosphorylation of the known PP2A substrate BAF. 3) The PP2A regulatory subunit Tws/B55 competes with Ankle2 for formation of a complex with PP2A. 4) AlphaFold3 predicts that Ankle2 engages in a complex with PP2A at a position similar to that of known regulatory subunits of PP2A including Tws/B55, and consistent with their mutually exclusive presence in PP2A complexes. If Ankle2 acted as a scaffold for the formation of a PP2A complex containing other regulatory subunits, we would expect to detect Ankle2 and another regulatory subunit in the same complex.

(3) Throughout the text, some conclusions are overstated or are not supported by data. Examples are below: 

a. Page 1: "we show for the first time that Ankle2 is a regulatory subunit of PP2A"  The authors show binding and changes in BAF phosphorylation levels, but changes in PP2A activity with modulation of Ankle2 weren't shown. 

We have replaced this phrase with this one:

“…we provide several lines of evidence that suggest that Ankle2 is a regulatory subunit of PP2A…”

b. Page 3: "The requirement for Ankle2 in the development of the central nervous system was initially discovered through its targeting by the microcephaly‐causing Zika virus (Shah et al.,

2018)." 

This is not the first paper showing ANKLE2 plays a role in the development of the CNS. Yamamoto et al., 2014 identified mutants in Ankle2 with defects in CNS development in flies and humans, establishing it as a human microcephaly‐causing gene. 

We are sorry for this oversight. We have now cited this important work.

c. Page 6: "Moreover, BAF appears to be the only obligatory substrate of Ankle2‐dependent dephosphorylation for cell proliferation as lowering the dose of the BAF kinase NHK‐1/Ballchen rescues wing development defects caused by the partial depletion of Ankle2 (Li et al., 2024)."  It is unclear why the authors conclude this since Ballchen/VRK1 can phosphorylate many things besides BAF. 

Although the conclusion cannot be drawn categorically, it seems to be by far the most likely scenario. However, we agree that in principle, other mechanisms could also account for these genetic observations, such as the dephosphorylation of another, still unidentified obligatory substrate of PP2A‐Ankle2 that would also be phosphorylated by NHK‐1/Ballchen. However, we have also shown that expression of an unphosphorylatable mutant form of BAF rescues phenotypes observed upon loss of Ankle2 function (Li et al, 2024). We have changed our sentence as follows:

"Moreover, BAF could be the only obligatory substrate of Ankle2‐dependent dephosphorylation for cell proliferation as lowering the dose of the BAF kinase NHK‐1/Ballchen or expression of an unphosphorylatable mutant form of BAF rescues wing development defects caused by the partial depletion of Ankle2 (Li et al., 2024).”

d. Page 10: "These results suggest that a Vap33‐Ankle2‐PP2A complex can mediate the recruitment of a pool of PP2A at the NE."

There is insufficient evidence to indicate that Vap33‐Ankle2‐PP2A exists in a stable state in the cell and that this complex mediates recruitment of PP2A at the NE. The images do not include Vap33, showing no evidence it is present when PP2A is at the NE and the complex could only be detected with overexpression. 

We agree with this caveat and recognize the need to be cautious when proposing our model. In this regard, we feel that our wording is reasonable and appropriate, using “suggest” rather than “prove”, “show” or “indicate”.

e. Page 11: These results suggest that the interaction of Ankle2 with PP2A is essential for its function in BAF dephosphorylation and nuclear reassembly." Page 14: "these results indicate that the interaction of Ankle2 with PP2A is essential during embryo". Page 14: "These results indicate that the interaction of Ankle2 with PP2A but not with Vap33 is essential for its function during cell proliferation in imaginal wing disc development." 

These experiments show that the ankyrin repeat in Ankle2 is necessary for these processes. It does not say PP2A interaction with Ankle2 is necessary because other things could bind the domain. 

We have revised the segments of the text mentioned, taking the reviewer’s legitimate concerns into consideration. We have also added the following sentence to the Discussion:

“However, it remains formally possible that the deletion of Ankyrin repeats used to disrupt the Ankle2‐PP2A interaction abrogated another, unknown aspect of Ankle2 function.”

f. Page 12: "Overall, we conclude that in addition to its N‐terminal PP2A‐interacting Ankyrin domain, Ankle2 requires the integrity of its C‐terminal portion for its essential function in nuclear reassembly." 

No data was shown for differences in nuclear reassembly, only the ability for ANKLE2 truncation mutants to localize to the nuclear envelope. It isn't clear whether the nuclear envelope reformation is normal in Figure S6 which the authors refer to. Lamin staining could help determine and conclude the C‐terminal region is important for nuclear envelope reformation. 

Our conclusion is drawn from the results shown in Figures S4 and S5 (described in the same section), where a rescue assay in cells was performed to assess the functionality of different variants of Ankle2‐GFP when endogenous Ankle2 was depleted. In this assay, Lamin and DNA staining were used to examine nuclear reassembly (as in Figure 5). Figure S6 shows the localizations of the different variants of Ankle2‐GFP, but endogenous Ankle2 is not depleted in these cells.

g. Page 13: "We conclude that the ability of Ankle2 to interact with PP2A is required for the timely recruitment of BAF at reassembling nuclei and ensuing NE reassembly."

It's possible the Ankyrin domain in ANKLE2 is interacting with proteins other than PP2A to recruit BAF at reassembling nuclei, especially since ANKLE2 is found to regulate VRK1 (Link 2019) which has been found to phosphorylate BAF during the cell cycle (Molitor 2014). Additionally, the images in Figure 6A appear to show fully reassembled nuclear envelopes in all mutants by 180s. 

This point relates to point e, raised above by this reviewer. We have re‐written the sentence as follows:

“We conclude that the Ankyrin domain, required for the ability of Ankle2 to interact with PP2A, is necessary for the timely recruitment of BAF at reassembling nuclei and ensuing NE reassembly.”

Please note that in this paragraph, we discuss a delay in RFP‐BAF recruitment, rather than the complete elimination of this recruitment. 

h. Page 16: "Our unbiased phosphoproteomic analysis confirmed that BAF dephosphorylation depends on Ankle2, despite the absence of a detectable interaction between Drosophila Ankle2 and BAF, which may be due to the lack of a LEM domain in the former (Fishburn et al., 2024). Moreover, while Ankle2 was shown to bind and inhibit the BAF counteracting kinase VRK1 in humans (Asencio et al., 2012), we detected no interaction between Ankle2 and NHK‐1/Ballchen (VRK1 ortholog) in Drosophila. This suggests that the loss of Ankle2 causes BAF hyperphosphorylation by preventing PP2A‐dependent dephosphorylation rather than by preventing inhibition of NHK‐1"

There could be transient binding between Ankle2 and Ballchen/VRK1/NHK‐1 or activity can be indirect, but that doesn't mean there is not a contribution of BAF phosphorylation by Ballchen/VRK1/NHK‐1. Genetic evidence from three model systems, including Drosophila, indicates there is a strong genetic interaction between Ankle2 and Ballchen/VRK1/NHK‐1 that includes rescue of lethality.

We agree and we have re‐written in this way:

“While a putative interaction between Ankle2 and NHK‐1 in Drosophila could occur transiently, thereby escaping detection, the simplest interpretation of our results is that the loss of Ankle2 causes BAF hyperphosphorylation by preventing PP2A‐dependent dephosphorylation rather than by preventing inhibition of NHK‐1.”

We do not question the fact that Ballchen/VRK1/NHK‐1 phosphorylates BAF and genetically interacts with Ankle2. The antagonistic relationship between Ballchen/VRK1/NHK‐1 and Ankle2 observed genetically can be explained by the fact that the kinase phosphorylates BAF while PP2AAnkle2 dephosphorylates it, without the need to invoke an additional inhibition of the kinase by Ankle2.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

The hypothesis is based on the idea that inversions capture genetic variants that have antagonistic effects on male sexual success (via some display traits) and survival of females (or both sexes) until reproduction. Furthermore, a sufficiently skewed distribution of male sexual success will tend to generate synergistic epistasis for male fitness even if the individual loci contribute to sexually selected traits in an additive way. This should favor inversions that keep these male-beneficial alleles at different loci together at a cis-LD. A series of simulations are presented and show that the scenario works at least under some conditions. While a polymorphism at a single locus with large antagonistic effects can be maintained for a certain range of parameters, a second such variant with somewhat smaller effects tends to be lost unless closely linked. It becomes much more likely for genomically distant variants that add to the antagonism to spread if they get trapped in an inversion; the model predicts this should drive accumulation of sexually antagonistic variants on the inversion versus standard haplotype, leading to the evolution of haplotypes with very strong cumulative antagonistic pleiotropic effects. This idea has some analogies with one of predominant hypotheses for the evolution of sex chromosomes, and the authors discuss these similarities. The model is quite specific, but the basic idea is intuitive and thus should be robust to the details of model assumption. It makes perfect sense in the context of the geographic pattern of inversion frequencies. One prediction of the models (notably that leads to the evolution of nearly homozygously lethal haplotypes) does not seem to reflect the reality of chromosomal inversions in Drosophila, as the authors carefully discuss, but it is the case of some other "supergenes", notably in ants. So the theoretical part is a strong novel contribution.

We appreciate the detailed and accurate summary of our main theoretic results.

To provide empirical support for this idea, the authors study the dynamics of inversions in population cages over one generation, tracking their frequencies through amplicon sequencing at three time points: (young adults), embryos and very old adult offspring of either sex (>2 months from adult emergence). Out of four inversions included in the experiment, two show patterns consistent with antagonistic effects on male sexual success (competitive paternity) and the survival of offspring, especially females, until an old age, which the authors interpret as consistent with their theory.

As I have argued in my comments on previous versions, the experiment only addresses one of the elements of the theoretical hypothesis, namely antagonistic effects of inversions on male reproductive success and other fitness components, in particular of females. Furthermore, the design of this experiment is not ideal from the viewpoint of the biological hypothesis it is aiming to test. This is in part because, rather than testing for the effects of inversion on male reproductive success versus the key fitness components of survival to maturity and female reproductive output, it looks at the effects on male reproductive success versus survival to a rather old age of 2 months. The relevance of survival until old age to fitness under natural conditions is unclear, as the authors now acknowledge. Furthermore, up to 15% of males that may have contributed to the next generation did not survive until genotyping, and thus the difference between these males' inversion frequency and that in their offspring may be confounded by this potential survival-based sampling bias. The experiment does not test for two other key elements of the proposed theory: the assumption of frequency-dependence of selection on male sexual success, and the prediction of synergistic epistasis for male fitness among genetic variants in the inversion. To be fair, particularly testing for synergistic epistasis would be exceedingly difficult, and the authors have now included a discussion of the above caveats and limitations, making their conclusions more tentative. This is good but of course does not make these limitations of the experiment go away. These limitations mean that the paper is stronger as a theoretical than as an empirical contribution.

We discuss the choice to focus on exploring the potential antagonistic effects of the inversion karyotype on male reproductive success and survival in our general response above. Primarily, this prediction seemed to be the most specific to the proposed model as compared to other alternate models. Still, further studies are clearly needed to elucidate the potential frequency dependence and genetic architecture of the inversions.

Regarding the choice of age at collection, it is unknown to what degree our selected collection age of 10 weeks correlates with survival in the wild, but we feel confident that there will be some positive correlation.

We now further clarify that across our experiments, a minimum of 5% and a mean of 9% of the males used in the parental generation died before collection. These proportions do not appear sufficient to explain the differences between paternal and embryo inversion frequencies shown in Figure 9.

Reviewer #2 (Public review):

Summary:

In their manuscript the authors address the question whether the inversion polymorphism in D. melanogaster can be explained by sexually antagonistic selection. They designed a new simulation tool to perform computer simulations, which confirmed their hypothesis. They also show a tradeoff between male reproduction and survival. Furthermore, some inversions display sex-specific survival.

Strengths:

It is an interesting idea on how chromosomal inversions may be maintained

Weaknesses:

The authors motivate their study by the observation that inversions are maintained in D. melanogaster and because inversions are more frequent closer to the equator, the authors conclude that it is unlikely that the inversion contributes to adaptation in more stressful environments. Rather the inversion seems to be more common in habitats that are closer to the native environment of ancestral Drosophila populations.

While I do agree with the authors that this observation is interesting, I do not think that it rules out a role in local adaptation. After all, the inversion is common in Africa, so it is perfectly conceivable that the non-inverted chromosome may have acquired a mutation contributing to the novel environment.

Based on their hypothesis, the authors propose an alternative strategy, which could maintain the inversion in a population. They perform some computer simulations, which are in line with the predicted behavior. Finally, the authors perform experiments and interpret the results as empirical evidence for their hypothesis. While the reviewer is not fully convinced about the empirical support, the key problem is that the proposed model does not explain the patterns of clinal variation observed for inversions in D. melanogaster. According to the proposed model, the inversions should have a similar frequency along latitudinal clines. So in essence, the authors develop a complicated theory because they felt that the current models do not explain the patterns of clinal variation, but this model also fails to explain the pattern of clinal variation.

To the contrary – in the Discussion paragraph beginning on Line 671, we explain why we would predict that a tradeoff between survival and reproduction should lead to clinal inversion frequencies. We suggest that a karyotype associated with a survival penalty should be increasingly disadvantageous in more challenging environments (such as high altitudes and latitudes for this species). Furthermore, an advantage in male reproductive competition conferred by that same haplotype may be reduced by the lower population densities that we would expect in more challenging environments (meaning that each female should encounter fewer males). Individually or jointly, these two factors predict that the equilibrium frequency of a balanced inversion frequency polymorphism should depend on a local population’s environmental harshness and population density, with the ensuing prediction that inversion frequency should correlate with certain environmental variables.

Reviewer #3 (Public review):

Summary:

In this study, McAllester and Pool develop a new model to explain the maintenance of balanced inversion polymorphism, based on (sexually) antagonistic alleles and a trade-off between male reproduction and survival (in females or both sexes). Simulations of this model support the plausibility of this mechanism. In addition, the authors use experiments on four naturally occurring inversion polymorphisms in D. melanogaster and find tentative evidence for one aspect of their theoretical model, namely the existence of the above-mentioned trade-off in two out of the four inversions.

Strengths:

(1) The study develops and analyzes a new (Drosophila melanogaster-inspired) model for the maintenance of balanced inversion polymorphism, combining elements of (sexually) antagonistically (pleiotropic) alleles, negative frequency-dependent selection and synergistic epistasis. Simulations of the model suggest that the hypothesized mechanism might be plausible.

(2) The above-mentioned model assumes, as a specific example, a trade-off between male reproductive display and survival; in the second part of their study, the authors perform laboratory experiments on four common D. melanogaster inversions to study whether these polymorphisms may be subject to such a trade-off. The authors observe that two of the four inversions show suggestive evidence that is consistent with a trade-off between male reproduction and survival.

Open issues:

(1) A gap in the current modeling is that, while a diploid situation is being studied, the model does not investigate the effects of varying degrees of dominance. It would thus be important and interesting, as the authors mention, to fill this gap in future work.

(2) It will also be important to further explore and corroborate the potential importance and generality of trade-offs between different fitness components in maintaining inversion polymorphisms in future work.

We appreciate the work put in to evaluating, improving, and summarizing our study. We agree that further work studying the effects of dominance and of the fitness components of the inversions is important.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

l. 354 : I don't understand what the authors mean by "an antagonistic and non-antagonistic allele". If there is a antagonistic polymorphism at a locus, then both alleles have antagonistic effects; i.e., allele B increases trait 1 and reduced trait 2 relative to allele A and vice versa.

Edited, agreed that the terminology used here was sub-optimal.

Reviewer #2 (Recommendations for the authors):

The motivation for their model is their claim that the clinal inversion frequencies are not compatible with local adaptation. The reviewer doubts this strong statement. Furthermore, the proposed model also fails to explain the inversion frequencies in natural populations.

Hence, rather than building a straw man, it would be better if the authors first show their experiments and then present their model as an explanation for the empirical results. Nevertheless, it is also clear that the empirical data are not very strong and cannot be fully explained by the proposed model.

This claim that we reject any role of local adaptation in clinal variation and selection upon inversion polymorphism does not hold up in a reading of our manuscript. We even suggest that locally varying selective pressures must be playing some role, although that does not imply that local adaptation is the ultimate driver of inversion frequencies. Indeed, we suggest that local adaptation alone is an insufficient explanation for inversion frequency clines in D. melanogaster, including because (1) these frequency clines do not approach the alternate fixed genotypes predicted by local directional selection, (2) these derived inversions tend to be more frequent in more ancestral environments (l.113-158).

In our public review response above, and in the Discussion section of our paper, we explain why our model can predict both the clinal frequencies of many Drosophila inversions and their intermediate maximal frequencies. Of course, we do not predict that most inversions in this species should follow the specific tradeoff investigated here. In fact, we were surprised to find even two inversions that experimentally supported our predicted tradeoff. Still, it remains possible that other inversions in this species are subject to other balanced tradeoffs not investigated here, which could help explain why they rarely reach high local frequencies.

Reviewer #3 (Recommendations for the authors):

My previous comments have been adequately addressed.

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

Reviewer #1 (Public Review):

[…]

To provide empirical support for this idea, the authors study the dynamics of inversions in population cages over one generation, tracking their frequencies through amplicon sequencing at three time points: (young adults), embryos and very old adult offspring of either sex (>2 months from adult emergence). Out of four inversions included in the experiment, two show patterns consistent with antagonistic effects on male sexual success (competitive paternity) and the survival of offspring, especially females, until an old age, which the authors interpret as consistent with their theory.

There are several reasons why the support from these data for the proposed theory is not waterproof.

(1) As I have already pointed out in my previous review, survival until 2 months (in fact, it is 10 weeks and so 2.3 months) of age is of little direct relevance to fitness, whether under natural conditions or under typical lab conditions.

The authors argue this objection away with two arguments

First, citing Pool (2015) they claim that the average generation time (i.e. the average age at which flies reproduce) in nature is 24 days. That paper made an estimate of 14.7 generations per year under the North Carolina climate. As also stated in Pool (2015), the conditions in that locality for Drosophila reproduction and development are not suitable during three months of the year. This yields an average generation length of about 19.5 days during the 9 months during which the flies can reproduce. On the highly nutritional food used in the lab and at the optimal temperature of 25 C, Drosophila need about 11-12 days to develop from egg to adult. Even assuming these perfect conditions, the average age (counted from adult eclosion) would be about 8 days. In practice, larval development in nature is likely longer for nutritional and temperature reasons, and thus the genomic data analyzed by Pool imply that the average adult age of reproducing flies in nature would be about 5 days, and not 24 days, and even less 10 weeks. This corresponds neatly to the 2-6 days median life expectancy of Drosophila adults in the field based on capture-recapture (e.g., Rosewell and Shorrocks 1987).

Second, the authors also claim that survival over a period of 2 month is highly relevant because flies have to survive long periods where reproduction is not possible. However, to survive the winter flies enter a reproductive diapause, which involves profound physiological changes that indeed allow them to survive for months, remaining mostly inactive, stress resistant and hidden from predators. Flies in the authors' experiment were not diapausing, given that they were given plentiful food and kept warm. It is still possible that survival to the ripe old age of 10 weeks under these conditions still correlates well with surviving diapause under harsh conditions, but if so, the authors should cite relevant data. Even then, I do not think this allows the authors to conclude that longevity is "the main selective pressure" on Drosophila (l. 936).

This is overall a thoughtfully presented critique and we have endeavored to improve our discussion of Pool (2015) and to clarify some of the language used about survival elsewhere. While we agree that challenges other than survival to 10 weeks are very relevant to Drosophila melanogaster, collection at 10 weeks does encompass some of these other challenges. Egg to adult viability still contributes to the frequencies of the inversions at collection and is not separable from longevity in this data. Collection at longevity was chosen in part to encompass all lifetime fitness challenges that might influence the inversion frequency at collection, albeit still within permissive laboratory conditions. Future experiments exploring specific stressors independently and beyond permissive lab conditions would generate a clearer picture.

In addition to general edits, the specific phrase mentioned at 1. 936 [now line 1003] has been revised from “In many such cases females are in reproductive diapause, and so longevity is the main selective pressure.” to “While longevity is a key selective pressure underlying overwintering, the relationship between longevity in permissive lab conditions without diapause and in natural conditions under diapause is unclear (Schmidt et al. 2005; Flatt 2020), and our experiment represents just one of many possible ways to examine tradeoffs involving survival.”

(2) It appears that the "parental" (in fact, paternal) inversion frequency was estimated by sequencing sires that survived until the end of the two-week mating period. No information is provided on male mortality during the mating period, but substantial mortality is likely given constant courtship and mating opportunities. If so, the difference between the parental and embryo inversion frequency could reflect the differential survival of males until the point of sampling rather than / in addition to sexual selection.

We have further clarified that when referenced as parental frequency, the frequency presented is ½ the paternal frequency as the mothers were homokaryotypic for the standard arrangement. We chose to present both due to considerations in representing the frequency change from paternal to embryo frequencies, where a hypothetical change from 0.20 frequency in fathers to 0.15 frequency in embryos represents a selective benefit (a frequency increase in the population), despite the reality that this is a decrease in allele frequency between paternal and embryo cohorts.

We mentioned a maximum 15% paternal mortality at line 827 [now l.1056], but have now added complete data on the counts of flies in the experiment as a supplemental table (Table S1) and have added or corrected further references to this in the results and methods [lines 555, 638, 975]. It is true that this may influence the observed frequency changes to some degree, and while we adjusted our sampling method to account for the effects of this mortality on statistical power [l.1056ff], we have now edited the manuscript to better highlight potential effects of this phenomenon on the recorded frequency changes.

It is also worth noting that, if mortality among fathers over the mating period is codirectional with mortality among aged offspring, this would bias the results against detecting an opposing antagonistic selective effect of the inversions on paternity share. This is now also mentioned in the manuscript, l.639ff.

(3) Finally, irrespective of the above caveats, the experimental data only address one of the elements of the theoretical hypothesis, namely antagonistic effects of inversions on reproduction and survival, notably that of females. It does not test for two other key elements of the proposed theory: the assumption of frequency-dependence of selection on male sexual success, and the prediction of synergistic epistasis for male fitness among genetic variants in the inversion. To be fair, particularly testing the latter prediction would be exceedingly difficult. Nonetheless, these limitations of the experiment mean that the paper is much stronger theoretical than empirical contribution.

This is a fair criticism of the limitations of our results, and we now summarize such caveats more directly in the discussion summary, lines 876ff.

Reviewer #2 (Public Review): 

[…]

Comments on the latest version:

I would like to give an example of the confusing terminology of the authors:

"Additionally, fitness conveyed by an allele favoring display quality is also frequency-dependent: since mating success depends on the display qualities of other males, the relative advantage of a display trait will be diminished as more males carry it..."

I do not understand the difference to an advantageous allele, as it increases in frequency the frequency increase of this allele decreases, but this has nothing to do with frequency dependent selection. In my opinion, the authors re-define frequency dependent selection, as for frequency dependent selection needs to change with frequency, but from their verbal description this is not clear.

We have edited this text for greater clarity, now line 232ff. We did not seek to redefine frequency dependence, and did mean by “the relative advantage of a display trait will be diminished” that an equivalent s would diminish with frequency. We have now remedied terminological issues introduced in the prior revision with regard to frequency dependent selection.

One example of how challenging the style of the manuscript is comes from their description of the DNA extraction procedure. In principle a straightforward method, but even here the authors provide a convoluted uninformative description of the procedure.

We have edited for clarity the text on lines 1016-1020. Citing a published protocol and mentioning our modifications seems an appropriate trade-off between representing what was done accurately, citing the sources we relied on in doing it, and limiting the volume of information in the main text for such a straightforward and common method. 

It is not apparent to the reviewer why the authors have not invested more effort to make their manuscript digestible.

We have invested a great deal of effort in making this manuscript as clear as we are able to.  We regret that our writing has not been to this reviewer’s liking. We believe we have been highly responsive to all specific criticisms, including revising all passages cited as unclear. In this round, we have again scrutinized the entire manuscript for any opportunity to clarify it, and we have made further changes throughout.  Although our subject matter is conceptually nuanced, we nevertheless remain optimistic that a careful, fresh reading of our revised manuscript would yield a more favorable impression.

Reviewer #3 (Public Review):

[…]

Weaknesses:

A gap in the current modeling is that, while a diploid situation is being studied, the model does not investigate the effects of varying degrees of dominance. It would be important and interesting to fill this gap in future work.

Agreed, and now reinforced at lines 892ff.

Comments on the latest version:

Most of the comments which I have made in my public review have been adequately addressed.

Some of the writing still seems somewhat verbose and perhaps not yet maximally succinct; some additional line-by-line polishing might still be helpful at this stage in terms of further improving clarity and flow (for the authors to consider and decide).

We have made further changes and some polishing in this draft, and greatly appreciate the guidance provided in improving the draft so far. 

Reviewer #1 (Recommendations For The Authors):

(1) While the model results are convincing, some of the verbal interpretation is confusing. In particular, the authors state that in their model the allele favoring male display quality shows a negative frequency dependence whereas the alternative allele has a positive frequency dependence. This does not make sense to me in the context of population genetics theory. For a one-locus, two-allele model the change of allele frequency under selection depends on the fitness of the genotypes concerned relative to each other. Thus, at least under no dominance assumed in this model, if the relative fitness of AA decreases with the frequency of allele A, the relative fitness of aa must decrease with the frequency of allele a. I.e., if selection is negatively frequency dependent, then it is so for both alleles.

This phrasing was wrong, and we have edited the relevant section.

(2) I am still not entirely sure that the synergistic epistasis assumed in the verbal model is actually generated in the simulations; this would be easy enough to check by extracting the mating success of males with different genotypes from the simulation output should be reported, e.g., as a figure supplement.

Our new Figure S2, which depicts haplotype frequencies for a set of the simulations presented in Figure 4, should demonstrate a necessary presence of synergistic epistasis. These results further clarify that the weaker allele B is only kept when linked to A. The same fitness classes of genotype are present in the simulations with and without the inversion, so the only mechanical difference is the rate of recombination, and the only way this might change selection on the alleles is if a variant has a different fitness in one haplotype background than another – i.e. epistasis. The maintenance of haplotypes AB and ab to the exclusion of Ab and aB relies on the lesser relative fitness of Ab and aB. And since survival values are multiplicative, this additional contribution must come from the mate success of AB being disproportionately larger than Ab or aB, indicating the emergent synergistic epistasis posited by our model. We have clarified this point in the text at line 363ff.

(3) l. 318ff: What was this set number of males? I could not find this information anywhere. Also, this model of the mating system is commonly referred to as "best of N", so the authors may want to include this label in the description.

We indicate this detail just after the referenced line, now reworded and on l. 338-340 as “For each female’s mating competition, 100 males were sampled, though see Figure S1 for plots with varying encounter number.”  Among these edits, “one hundred” has been changed to a numeral for easier skimming, and Figure S1 is now referenced here earlier in the text. Several edits have also been made in the caption of Figures 2 and 3, and in the relevant methods section to clarify the number of encountered males simulated, mention best of N terminology, and clarify how the quality score is used in the mate competition.

(4) The description of the experiment is still confusing. The number of individuals of each sex entered in each mating cage is missing from the Methods (l. 914); although I did finally find it in the Results. These flies were laying over 2 weeks - does this mean that offspring from the entire period were used to obtain the embryo and aged offspring frequencies, or only from a particular egg collection? If the former, does this mean that the offspring obtained from different egg batches were aged separately? Were the offspring aged in cages or bottles, at what density? Given that only those males that survived until the end of the two-week mating period were sequenced, it is important to know what % of the initial number of males these survivors were. A substantial mortality of the parental males could bias the estimate of parental frequencies. How many parental males, embryos and aged offspring were sequenced? Were all individuals of a given cage and stage extracted and sequenced as a single pool or were there multiple pools? The description could also be structured better. For example, the food and grape agar recipes and cage construction are inserted at random points of the description of the crossing design, which does not help.

We have now reorganized and edited these portions of the Methods text. Portions of this comment overlap with edits responding to (2) of the Public Review and below for l. 921 in Details. Offspring from different laying periods were aged in different bottles, further separated by the time at which they eclosed. They were then pooled for DNA extraction and library preparation by sex and a binary early or late eclosion time. This data was present in the “D. mel. Sample Size” column of supplemental tables S6 and S7 (now S7 and S8), but we have added and referenced a new table to specifically collate the sample sizes of different experimental stages, table S1. Now referenced at lines 555, 638, 975, 1057.

(5) The caption of figure 9 and the discussion of its results should be clear and explicit about the fact that "adult offspring" in Fig 9A and "female" and "male" refers to adults surviving to old age (whereas "parental" in Fig 9A refers to young adults in their reproductive prime. This has consequences for the interpretation of the difference between "parental" and "adult offspring", as it combines one generation of usual selection as it occurs under the conditions of the lab culture (young adult at generation t -> young adult in generation t+1) with an additional step of selection for longevity. Thus, a marked change in allele frequency does not imply that the "parental" frequency does not represent an equilibrium frequency of the inversions under the lab culture conditions. Furthermore, it would be useful to state explicitly that Figure 9B represents the same results as figure 9A, but with the aged offspring split by sex.

Figure caption edited to provide further clarity on the age of cohorts and presented data, along with the relevant results section (2.3) referencing this figure.

We avoid making any statements about the equilibrium frequencies of inversions under lab conditions, and whether or not any step of our experiment reflects such equilibria, because our investigation does not rely upon or test for such conditions. Instead, our analysis focuses on whether inversions have contrasting effects (as indicated by frequency changes that are incompatible with neutral sampling) between different life history components.  Under our model, such frequency reversals might be detectable both at equilibrium balanced inversion frequencies and also at frequencies some distance away from equilibria. We have now clarified this point at l. 970-972.

Details:

l. 211: this should be modified as male-only costs are now included.

Edited. “survival likelihood (of either or both sexes).”

l. 343: misplaced period

Edited.

l. 814: "We confirmed model predictions...": This sounds like it refers to an empirical confirmation of a theory prediction, but I think the authors just want to say that their simulations predicted antagonistic variants can be maintained at an intermediate equilibrium frequency. So the wording should be changed to avoid ambiguity.

Edited. Now line 869.

l. 853: How can a genome be "empty"? Do the authors mean an absence of any polymorphism?

Edited to: “In SAIsim, a population is instantiated as a python object, and populated with individuals which are also represented by python objects. These individuals may be instantiated using genomes specified by the user, or by default carry no genomic variation.” Lines 913ff.

l. 853: I do not see this diagramed in Figure 5

Apologies, fixed to Fig. 2

l. 864: is crossing-over in the model limited to female gametogenesis (reflecting the Drosophila case) or does it occur in both sexes?

There is a variable in the simulator to make crossover female-specific. All simulations were performed with female-only crossover. Edited for clarity. “While the simulator can allow recombination in both sexes, all simulations presented only generate crossovers and gene conversion events for female gametes, in accordance with the biology of D. melanogaster.” Lines 928-929.

l. 906: "F2" is ambiguous; does this mean that the mix of lines was allowed to breed for two generations? Also, in other places in the manuscript these flies appear to be referred to are "parental". So do not use F2.

Edited, F2 language removed and replaced with being allowed to breed for two generations. Now lines 967ff.

l. 910: this is incorrect/imprecise; what can be inferred is the frequency of the inversions in male gametes that contributed to fertilization. This would correspond to the frequency in successful males only if each successful male genotype had the same paternity share.

Edited, now “Since no inversions could be inherited through the mothers, inversion frequencies among successful male gametes could be inferred from their pooled offspring.” Now line 994.

l. 912: "without a controlled day/night cycle" meaning what? Constant light? Constant darkness? Daylight falling through the windows?

Edited to “Unless otherwise noted, all flies were kept in a lab space of 23°C with around a degree of temperature fluctuation and without a controlled day/night cycle. Light exposure was dependent on the varying use of the space by laboratory workers but amounted to near constant exposure to at least a minimal level of lighting, with some variable light due to indirect lighting from adjacent rooms with exterior windows.” Now lines 1007-1010.

l. 921: I cannot parse this sentence. Were the offspring isolated as virgins?

No, the logistics of collecting virgins would have been prohibitive, and it did not seem essential for our experiment. Hopefully the edits to this section are clearer, now lines 978ff.

Author response:

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

Reviewer 1 (Public Comments):

(1) The central concern for this manuscript is the apparent lack of reproducibility. The way the authors discuss the issue (lines 523-554) it sounds as though they are unable to reproduce their initial results (which are reported in the main text), even when previous versions of AlphaFold2 are used. If this is the case, it does not seem that AlphaFold can be a reliable tool for predicting antibody-peptide interactions.

The driving point behind the multiple sequence alignment (MSA) discussion was indeed to point out that AlphaFold2 (AF2) performance when predicting scFv:peptide complexes is highly dependent upon the MSA, but that is a function of MSA generation algorithm (MMseqs2, HHbiltz, jackhmmer, hhsearch, kalign, etc) and sequence databases, and less an intrinsic function of AF2. It is important to report MSA-dependent performance precisely because this results in changing capabilities with respect to peptide prediction.

Performance also significantly varies with the target peptide and scFv framework changes. By reporting the varying success rates (as a function of MSA, peptide target, and framework changes) we aim to help future researchers craft modified algorithms that can achieve increased reliability at protein-peptide binding predictions. Ultimately, tracking down how MSA generation details vary results (especially when the MSA’s are hundreds long) is significantly outside the scope of this paper. Our goal for this paper was to show a general method for identification of linear antibody epitopes using only sequence information, and future work by us or others should focus on optimization of the process. 

(2) Aside from the fundamental issue of reproducibility, the number of validating tests is insufficient to assess the ability of AlphaFold to predict antibody-peptide interactions. Given the authors' use of AlphaFold to identify antibody binding to a linear epitope within a whole protein (in the mBG17:SARS-Cov-2 nucleocapsid protein interaction), they should expand their test set well beyond Myc- and HA-tags using antibody-antigen interactions from existing large structural databases.

Performing the calculations at the scale that the reviewer is requesting is not feasible at this time. We showed in this manuscript that we were able to predict 3 of 3 epitopes, including one antigen and antibody pair that have not been deposited into the PDB with no homologs. While we feel that an N=3 is acceptable to introduce this method to the scientific community, we will consider adding more examples of success and failure in the future to optimize and refine the method as computational resources become available. Notably, future efforts that attempt high-throughput predictions of this class using existing databases should take particular care to avoid contamination.

(3) As discussed in lines 358-361, the authors are unsure if their primary control tests (antibody binding to Myc-tag and HA-tag) are included in the training data. Lines 324-330 suggest that even if the peptides are not included in the AlphaFold training data because they contain fewer than 10 amino acids, the antibody structures may very well be included, with an obvious "void" that would be best filled by a peptide. The authors must confirm that their tests are not included in the AlphaFold training data, or re-run the analysis with these templates removed.

First, we address the simpler question of templates.

The reruns of AF2 with the local 2022 rebuild, the most reproducible method used with results most on par with the MMSEQS server in the Fall of 2022, were run without templates. This is because the MSA was generated locally; no templates were matched and generated locally. The only information passed then was the locally generated MSA, and the fasta sequence of the unchanging scFv and the dynamic epitope sequence. Because of how well this performed despite the absence of templates, we can confidently say the inclusion of the template flag is not significant with respect to how universally accurately PAbFold can identify the correct epitope. 

Second, we can partially address the question of whether the AlphaFold models had access to models suitable, in theory, for “memorization” of pertinent structural details. 

With respect to tracking the exact role and inclusion of specific PDB entries, the AF2 paper provides the following:

“Structures from the PDB were used for training and as templates (https://www.wwpdb.org/ftp/pdb-ftp-sites; for the associated sequence data and 40% sequence clustering see also https://ftp.wwpdb.org/pub/pdb/derived_data/ and https://cdn.rcsb.org/resources/sequence/clusters/bc-40.out). Training used a version of the PDB downloaded 28 August 2019, while the CASP14 template search used a version downloaded 14 May 2020. The template search also used the PDB70 database, downloaded 13 May 2020 (https://wwwuser.gwdg.de/~compbiol/data/hhsuite/databases/hhsuite_dbs/).”

Three of these links are dead. As such, it is difficult to definitively assess the role of any particular PDB entry with respect to AF2 training/testing, nor what impact homologous training structures given the very large number of immunoglobin structures in the training set. That said, we can summarize information for the potentially relevant PDB entries (l 2or9, which is shown in Fig. 1 and 1frg), and believe it is most conservative to assume that each such entry was within the training set.

PDB entry 2or9 (released 2008): the anti-c-myc antibody 9E10 Fab fragment in complex with an 11-amino acid synthetic epitope: EQKLISEEDLN. This crystal structure is also noteworthy for featuring a binding mode where the peptide is pinned between two Fab. The apo structure (2orb) is also in the database but lacks the peptide and a resolved structure for CDR H3.

PDB entry 1a93 (released 1998): a c-Myc-Max leucine zipper structure, where the c-Myc epitope (in a 34-amino acid protein) adopts an alpha helical conformation completely different from the epitope captured in entry 2or9.

PDB entries 5xcs and 5xcu (released 2017): engineered Fv-clasps (scFv alternatives) in complex with the 9-amino acid synthetic HA epitope: YPYDVPDYA.

PDB entry 1frg (released 1994): anti-HA peptide Fab in complex with HA epitope subset Ace-DVPDYASL-NH2.

Since the 2or9 entry has our target epitope (10 aa) embedded within an 11aa sequence, we have revised this line in the manuscript:

The AlphaFold2 training set was reported to exclude chains of less than 10, which would eliminate the myc and HA epitope peptides. => The AlphaFold2 training set was reported to exclude chains of less than 10, which would eliminate the HA epitope peptide from potential training PDB entries such as 5xcs or 5xcu”

It is important to note that we obtained the best prediction performance for the scFv:peptide pair that had no pertinent PDB entries (mBG17). Specifically, doing a Protein Blast against the PDB using the mBG17 scFv revealed diverse homologs, but a maximum sequence identity of 89.8% for the heavy chain (to an unrelated antibody) and 93.8% for the light chain (to an unrelated antibody). Additionally, while it is possible that the AF2 models might have learned from the complex in pdb entry 2or9, Supplemental Figure 3 shows how often the peptide is “misplaced”, and the performance does not exceed the performance for mBG17.

(4) The ability of AlphaFold to refine the linear epitope of antibody mBG17 is quite impressive and robust to the reproducibility issues the authors have run into. However, Figure 4 seems to suggest that the target epitope adopts an alpha-helical structure. This may be why the score is so high and the prediction is so robust. It would be very useful to see along with the pLDDT by residue plots a structure prediction by residue plot. This would help to see if the high confidence pLDDT is coming more from confidence in the docking of the peptide or confidence in the structure of the peptide.

The reviewer is correct that target mBG17 epitope adopts an alpha helical conformation, and we concur that this likely contributes to the more reliable structure prediction performance.  When we predict the structure of the epitope alone without the mBG17 scFv, AF2 confidently predicts an alpha helix with an average pLDDT of 88.2 (ranging from 74.6 to 94.4). 

Author response image 1.

The AF2 prediction for the mBG17 epitope by itself.

However, as one interesting point of comparison, a 10 a.a. poly-alanine peptide is also consistently folded into an alpha-helical coil by AF2. The A₁₀ peptide is also predicted to bind among the traditional scFv CDR loops, but the pLDDT scores are very poor (Supplemental Figure 5J). We also observed the opposite case; when a peptide has a very unstructured region in the binding domain but is nonetheless still be placed confidently, as seen in Supplemental Figure 3 C&D. Therefore, while we suspect peptides with strong alpha helical propensity are more likely to be accurately predicted, the data suggests that that alpha helix adoption is neither necessary nor sufficient to reach a confident prediction.

(5) Related to the above comment, pLDDT is insufficient as a metric for assessing antibody antigen interactions. There is a chance (as is nicely shown in Figure S3C) that AlphaFold can be confident and wrong. Here we see two orange-yellow dots (fairly high confidence) that place the peptide COM far from the true binding region. While running the recommended larger validation above, the authors should also include a peptide RMSD or COM distance metric, to show that the peptide identity is confident, and the peptide placement is roughly correct. These predictions are not nearly as valuable if AlphaFold is getting the right answer for the wrong reasons (i.e. high pLDDT but peptide binding to a nonCDR loop region). Eventual users of the software will likely want to make point mutations or perturb the binding regions identified by the structural predictions (as the authors do in Figure 4).

We agree with the reviewer that pLDDT is not a perfect metric, and we are following with great interest the evolving community discussion as to what metrics are most predictive of binding affinity (e.g. pAE, or pITM as a decent predictor for binding, but not affinity ranking). To our knowledge, there is not yet a consensus for the most predictive metrics for protein:protein binding nor protein:peptide binding. Intriguingly, since the antigen peptides are so small in our case, the pLDDT of the peptide residues should be mostly reporting on the confidence of the distances to neighboring protein residues.

As to the suggestion for a RMSD or COM distance metric, we agree that these are useful -with the caveat that these require a reference structure. The goal of our method is to quickly narrow down candidate linear epitopes and thereby guide experimentalists to more efficiently determine the actual binding sequence of an antibody-antigen sequence. Presumably this would not be necessary if a reference structure were known. 

It may also be possible to invent a method to filter unlikely binding modes that is specific to antibodies and peptide epitopes that does not require a known reference structure, but this would be an interesting problem for subsequent study.

Reviewer 1 (Recommendations for the Authors):

(1) "Linear epitope" should be more precisely defined in the text. It isn't clear whether the authors hope that they can use AlphaFold to predict where on a given protein antigen an antibody will bind, or which antigenic peptide the antibody will bind to. The authors discuss both problems, and there is an important distinction between the two. If the authors are only concerned with isolated antigenic peptides, rather than linear epitopes in their full length structural contexts, they should be more precise in the introduction and discussion.

We thank the reviewer for the prompt towards higher precision. We are using the short contiguous antigen definition of “linear epitope” that depends on secondary rather than tertiary structure. The linear epitopes this paper considers are short “peptides” that form secondary structure independent of their structure in the complete folded antigen protein. We have clarified our definition of “linear epitope” in the text (lines 64-66). 

(2) Line 101: "Not all portions of the antibody are critical". First, this is not consistent with the literature, particularly where computational biology is concerned.

See https://pubs.acs.org/doi/10.1021/acs.jctc.7b00080 . Second, while I largely agree with what I think the authors are trying to say (that we can largely reduce the problem to the CDR loops), this is inconsistent with what the authors later find, which is that inexplicably the VH/VL scaffold used alters results strongly.

We have adopted verbiage that should be less provocative: “Fortunately, with respect to epitope specificity, antibody constant domains are less critical than the CDR loops and the remainder of the variable domain framework regions.”

(3) Related to the above comment, do the authors have any idea why epitope prediction performance improved for the chimeric scFvs? Is this due to some stochasticity in AlphaFold? Or is there something systematic? Expanding the test dataset would again help answer this question.

We agree that future study with a larger test set could help address this intriguing result, for which we currently lack a conclusive explanation. Part of our motivation for this publication was to bring to light this unexpected result. Notably, these framework differences are not only implicated as a factor in driving AF2 performance, but also changing experimental intracellular performance as reported by our group (DOI: 10.1038/s41467-019-10846-1 ). We can generate a variety of hypotheses for this phenomenon. Just as MSA sub-sampling has been a popular approach to drive AF2 to sample alternative conformations, sequence recombination may be a generically effective way to generate usefully different binding predictions. However, it is difficult to discriminate between recombination inducing subtle structural tweaks that increase protein intracellular fitness and binding, from recombination causing changes to the MSA that affect the likelihood of sampling a good epitope binding conformation. It is also possible that the chimeras are more deftly predicted by AF2 due to differences in sequence representation during the training of the AF2 models (e.g. more exposure to models containing 15F11 or 2E2 structures). We attempted to deconvolute MSA differences by using single-sequence mode (Supplementary Figure 13) but this ablated performance.

(4) Figure 2: The reported consensus pLDDT scores are actually quite low here, suggesting low confidence in the result. This is in strong contrast to the reported consensus scores for mBG17. Again, a larger test dataset would help set a quantitative cutoff for where to draw the line for "trustworthy" AlphaFold predictions in antibody-peptide binding applications.

We agree that a larger dataset will be useful to begin to establish metrics and thresholds and will contribute to the aforementioned community discussion about reliable predictors of binding. Our current focus is not structure prediction per se. In the current work we are more focused on relative binding likelihood and increasing the efficiency of experimental epitope verification by flagging the most likely linear epitopes. Thus, while the pLDDT scores are low for Myc in Figure 2, it is remarkable (and worth reporting) that there is still useful signal in the relative variation in pLDDT. The utility of the signal variation is evident in the ability to short-list correct lead peptides via the two methods we demonstrate (consensus and per-residue max).

(5) Figure 4: if the authors are going to draw conclusions from the actual structure predictions of AlphaFold (not just the pLDDT scores), the side-chain accuracy placement should be assessed in the test dataset (RMSD or COM distance).

We agree with the reviewer that side-chain placement accuracy is important when evaluating the accuracy of AF2 structure predictions. However, here our focus was relative binding likelihood rather than structure prediction. The one case where we attempted to draw conclusions from the structure prediction was in the context of mBG17, where there is not yet an experimental reference structure. Absolutely, if we were to obtain a crystal structure for that complex, we would assess side-chain placement accuracy. 

(6) Lines 493-508: I am not sure that this assessment for why AlphaFold has difficulty with antibody-antigen interactions is correct. If the authors' interpretation is correct (larger complicated structures are more challenging to move) then AlphaFold-Multimer (https://www.biorxiv.org/content/10.1101/2021.10.04.463034v2.full) wouldn't perform as well as it does. Instead, the issue is likely due to the incredibly high diversity in antibody CDR loops, which reduces the ability of the AlphaFold MSA step (which the authors show is quite critical to predictions: Figure S13) to inform structure prediction. This, coupled with the importance of side chain placement in antibody and TCR interactions, which is notoriously difficult (https://elifesciences.org/articles/90681), are likely the largest source of uncertainty in antibody-antigen interaction prediction.

We agree with the reviewer that CDR loop diversity (and associated side chain placement challenges) are a major barrier to successfully predict antibody-antigen complexes. Presumably this is true for both peptide antigens and protein antigens. Indeed, the authors of AlphaFold-multimer admit that the updated model struggles with antibody-antigen complexes, saying “As a limitation, we observe anecdotally that AlphaFold-Multimer is generally not able to predict binding of antibodies and this remains an area for future work.” The point about how loop diversity could reduce MSA quality is well taken. We have included the following thanks to the guidance of the reviewer when discussing MSA sensitivity is discussed later on in lines 570-572.: 

“These challenges are presumably compounded by the incredible diversity of the CDR loops in antibodies which could decrease the useful signal from the MSA as well as drive inconsistent MSA-dependent performance”.

With respect to lines 493-508, we have also rephrased a key sentence to try to better explain that we are comparing the often-good recognition performance for short epitopes to the never-good performance when those epitopes are embedded within larger sequences. Instead of saying, “In contrast, a larger and complicated structure may be more challenging to move during the AlphaFold2 structure prediction or recycle steps.” we now say in lines 520-522 , “In contrast, embedding the epitope within a larger and more complicated structure appears to degrade the ability of AlphaFold2 to sample a comparable bound structure within the allotted recycle steps.”

(7) Related to major comment 1: Are AlphaFold predictions deterministic? That is, if you run the same peptide through the PAbFold pipeline 20 times, will you get the same pLDDT score 20 times? The lack of reproducibility may be in part due to stochasticity in AlphaFold, which the authors could actually leverage to provide more consistent results.

This is a good question that we addressed while dissecting the variable performance. When the random seed is fixed, AF2 returns the same prediction every time. After running this 10 times with a fixed seed, the mBG17 epitope was predicted with an average pLDDT of 88.94, with a standard deviation of 1.4 x 10^-14. In contrast, when no seed is specified, AF2 did not return an *identical* result. However, the results were still remarkably consistent. Running the mBG17 epitope prediction 10 times with a different seed gave an average pLDDT of 89.24, with a standard deviation of 0.49. 

(8) Related to major comment 2: The authors could use, for example, this previous survey of 1833 antibody-antigen interactions (https://www.sciencedirect.com/science/article/pii/S2001037023004725) the authors could likely pull out multiple linear epitopes to test AlphaFold's performance on antibody peptide interactions. A large number of tests are necessary for validation.

We thank the reviewer for this report of antibody-antigen interactions and will use it as a source of complexes in a future expanded study. Given the quantity and complexity of the data that we are already providing, as well as logistical challenges for compute and personnel the reviewer is asking for, we must defer this expansion to future work.

(9) Related to major comment 3: Apologies if this is too informal for a review, but this Issue on the AlphaFold GitHub may be useful: https://github.com/googledeepmind/alphafold/issues/416 .

We thank the reviewer for the suggestion – per our response above we have indeed run predictions with no templates. Since we are using local AlphaFold2 calculations with localcolabfold, the use or non-use of templates is fairly simple: including a “—templates” flag or not.

(10) Related to major comment 4: I am not sure if AlphaFold outputs by-residue secondary structure prediction by default, but I know that Phyre2 does http://www.sbg.bio.ic.ac.uk/~phyre2/html/page.cgi?id=index .

To our knowledge, AF2 does not predict secondary structure independent of the predicted tertiary structure. When we need to analyze the secondary structure we typically use the program DSSP from the tertiary structure. 

(11) The documentation for this software is incomplete. The GitHub ReadMe should include complete guidelines for users with details of expected outputs, along with a thorough step-by-step walkthrough for use.

We thank the reviewer for pointing this out, but we feel that the level of detail we provide in the GitHub is sufficient for users to utilize the method described.

Stylistic comments:

(1) I do not think that the heatmaps (as in 1C, top) add much information for the reader. They are largely uniform across the y-axis (to my eyes), and the information is better conveyed by the bar and line graphs (as in 1C, middle and bottom panels).

We thank the reviewer for this feedback but elect to leave it in on the premise of more data presented is (usually) better. Including the y-axis reveals common patterns such as the lower confidence of the peptide termini, as well as the lack of some patterns that might have occurred. For example, if a subset of five contiguous residues was necessary and sufficient for local high confidence this could be visually apparent as a “staircase” in the heat map.

(2) A discussion of some of the shortcomings of other prediction-based software (lines 7177) might be useful. Why are these tools less well-equipped than AlphaFold for this problem? And if they have tried to predict antibody-antigen interactions, why have they failed?

We agree with the reviewer that a broader review of multiple methods would be interesting and useful. One challenge is that the suite of available methods is evolving rapidly, though only a subset work for multimeric systems. Some detail on deficiencies of other approaches was provided in lines 71-77 originally, although we did not go into exhaustive detail since we wanted to focus on AF2. We view using AF2 in this manner is novel and that providing additional options predict antibody epitopes will be of interest to the scientific community. We also chose AF2 because we have ample experience with it and is a software that many in the scientific community are already using and comfortable with. Additionally, AF2 provided us with a quantification parameter (pLDDT) to assess the peptides’ binding abilities. We think a future study that compares the ability of multiple emerging tools for scFv:peptide prediction will be quite interesting. 

(3) Similar to the above comment, more discussion focused on why AlphaFold2 fails for antibodies (lines 126-128) might be useful for readers.  

We thank the reviewer for the suggestion. The following line has been added shortly after lines 135-137:

“Another reason for selecting AF2 is to attempt to quantify its abilities the compare simple linear epitopes, since the team behind AF-multimer reported that conformational antibody complexes were difficult to predict accurately (14).”

Per earlier responses, we also added text that flags one particular possible reason for the general difficulty of predicting antibody-antigen complexes (the diversity of the CDR loops and associated MSA challenges).

(4) The first two paragraphs of the results section (lines 226-254) could likely be moved to the Methods. Additionally, details of how the scores are calculated, not just how the commands are run in python, would be useful.

Per the reviewer suggestion, we moved this section to the end of the Methods section. Also, to aid in the reader’s digestion of the analysis, the following text has been added to the Results section (lines 256-264):

“Both the ‘Simple Max’ and ‘Consensus’ methods were calculated first by parsing every pLDDT score received by every residue in the antigen sequence sliding window output structures. From the resulting data structure, the Simple Max method simply finds the maximum pLDDT value ever seen for a single residue (across all sliding windows and AF2 models). For the Consensus method, per-residue pLDDT was first averaged across the 5 AF2 models. These averages are reported in the heatmap view, and further averaged per sliding window for the bar chart below.

In principle, the strategy behind the Consensus method is to take into account agreement across the 5 AF2 models and provide insight into the confidence of entire epitopes (whole sliding windows of n=10 default) instead of disconnected, per-residue pLDDT maxima.” 

(5) Figure 1 would be more useful if you could differentiate specifically how the Consensus and Simple Max scoring is different. Providing examples for how and why the top 5 peptide hits can change (quite significantly) using both methods would greatly help readers understand what is going on.

Per the reviewer suggestion, we have added text to discuss the variable hit selection that results from the two scoring metrics. The new text (lines 264-271) adds onto the added text block immediately above:

“Having two scoring metrics is useful because the selection of predicted hits can differ. As shown in Figure 2, part of the Myc epitope makes it into the top 5 peptides when selection is based on summing per-residue maximum pLDDT (despite there being no requirement that these values originate in the same physical prediction). In contrast, a Consensus method score more directly reports on a specific sliding window, and the strength of the highest confidence peptides is more directly revealed with superior signal to noise as shown in Figure 3. Variability in the ranking of top hits between the two methods arises from the fundamental difference in strategy (peptide-centric or residue-centric scoring) as well as close competition between the raw AF2 confidence in the known peptide and competing decoy sequences.”

(6) Hopefully the reproducibility issue is alleviated, but if not the discussion of it (lines 523554) should be moved to the supplement or an appendix.

The ability of the original AF2 model to predict protein-protein complexes was an emergent behavior, and then an explicit training goal for AF2.multimer. In this vein, the ability to predict scFv:peptide complexes is also an emergent capability of these models. It is our hope that by highlighting this capacity, as well as the high level of sensitivity, that this capability will be enhanced and not degraded in future models/algorithms (both general and specialized). In this regard, with an eye towards progress, we think it is actually important to put this issue in the scientific foreground rather than the background. When it comes to improving machine learning methods negative results are also exceedingly important.

Reviewer 2 (Recommendations for the Author):

- Line 113, page 3 - the structures of the novel scFv chimeras can be rapidly and confidently be predicted by AlphaFold2 to the structures of the novel scFv chimeras can be rapidly and confidently predicted by AlphaFold2.

The superfluous “be” was removed from the text.

- Line 276 and 278 page 9 - peptide sequences QKLSEEDLL and EQKLSEEDL in the text are different from the sequences reported in Figures 1 and 2 (QKLISEEDLL and EQKLISEEDL). Please check throughout the manuscript and also in the Figure caption (as in Figure 2).

These changes were made throughout the text. 

- I would include how you calculate the pLDDT score for both Simple Max approach and Consensus analysis.

Good suggestion, this should be covered via the additions noted above.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Rigor in the design and application of scientific experiments is an ongoing concern in preclinical (animal) research. Because findings from these studies are often used in the design of clinical (human) studies, it is critical that the results of the preclinical studies are valid and replicable. However, several recent peer-reviewed published papers have shown that some of the research results in cardiovascular research literature may not be valid because their use of key design elements is unacceptably low. The current study is designed to expand on and replicate previous preclinical studies in nine leading scientific research journals. Cardiovascular research articles that were used for examination were obtained from a PubMed Search. These articles were carefully examined for four elements that are important in the design of animal experiments: use of both biological sexes, randomization of subjects for experimental groups, blinding of the experimenters, and estimating the proper size of samples for the experimental groups. The findings of the current study indicate that the use of these four design elements in the reported research in preclinical research is unacceptably low. Therefore, the results replicate previous studies and demonstrate once again that there is an ongoing problem in the experimental design of preclinical cardiovascular research.

Strengths:

This study selected four important design elements for study. The descriptions in the text and figures of this paper clearly demonstrate that the rate of use of all four design elements in the examined research articles was unacceptably low. The current study is important because it replicates previous studies and continues to call attention once again to serious problems in the design of preclinical studies, and the problem does not seem to lessen over time.

Weaknesses:

The current study uses both descriptive and inferential statistics extensively in describing the results. The descriptive statistics are clear and strong, demonstrating the main point of the study, that the use of these design elements is quite low, which may invalidate many of the reported studies. In addition, inferential statistical tests were used to compare the use of the four design elements against each other and to compare some of the journals. The use of inferential statistical tests appears weak because the wrong tests may have been used in some cases. However, the overall descriptive findings are very strong and make the major points of the study.

We sincerely appreciate the reviewer’s comments and detailed feedback and their recognition of the importance of this work in replicating previous studies and calling attention to the problems in preclinical study design. In response to the reviewer’s suggestions, we have recalculated our inferential statistics. In place of our previous inferential statistics, we have used an alternative correction calculation for p-values (Holm-Bonferroni corrections) and used median-based linear model analyses and nonparametric Kruskal-Wallis tests that are more appropriate for analyzing this dataset. Our overall trends in results remain the same.

Reviewer #2 (Public Review):

Summary

This study replicates a 2017 study in which the authors reviewed papers for four key elements of rigor: inclusion of sex as a biological variable, randomization of subjects, blinding outcomes, and pre-specified sample size estimation. Here they screened 298 published papers for the four elements. Over a 10 year period, rigor (defined as including any of the 4 elements) failed to improve. They could not detect any differences across the journals they surveyed, nor across models. They focused primarily on cardiovascular disease, which both helps focus the research but limits the potential generalizability to a broader range of scientific investigation. There is no reason, however, to believe rigor is any better or worse in other fields, and hence this study is a good 'snapshot' of the progress of improving rigor over time.

Strengths

The authors randomly selected papers from leading journals, e.g., PNAS). Each paper was reviewed by 2 investigators. They pulled papers over a 10-year period, 2011 to 2021, and have a good sample of time over which to look for changes. The analysis followed generally accepted guidelines for a structured review.

Weaknesses

The authors did not use the exact same journals as they did in the 2017 study. This makes comparing the results complicated. Also, they pulled papers from 2011 to 2021, and hence cannot assess the impact of their own prior paper.

The authors write "the proportion of studies including animals of both biological sexes generally increased between 2011 and 2021, though not significantly (R2= 0.0762, F(1,9)= 0.742, p= 0.411 (corrected p=8.2". This statement is not rigorous because the regression result is not statistically significant. Their data supports neither a claim of an increase nor a decrease over time. A similar problem repeats several times in the remainder of their results presentation.

I think the Introduction and the Discussion are somewhat repetitive and the wording could be reduced.

Impact and Context

Lack of reproducibility remains an enormous problem in science, plaguing both basic and translational investigations. With the increased scrutiny on rigor, and requirements at NIH and other funding agencies for more rigor and transparency, one would expect to find increasing rigor, as evidenced by authors including more study design elements (SDEs) that are recommended. This review found no such change, and this is quite disheartening. The data implies that journals-editors and reviewers-will have to increase their scrutiny and standards applied to preclinical and basic studies. This work could also serve as a call to action to investigators outside of cardiovascular science to reflect on their own experiences and when planning future projects.

We sincerely appreciate the reviewer’s insights and comments and recognition of our work contributing to the growing body of evidence on the lack of rigor in preclinical cardiovascular research study design. Regarding the weaknesses the reviewer noted; the referenced 2017 publication details a study by Ramirez et al, and was not conducted by our group. Our study aimed to expand upon their findings by using a more recent timeframe and an alternative list of highly respected cardiovascular research journals. We have now better clarified this distinction in the manuscript. We have also addressed our phrasing regarding the lack of statistical significance in the increase of the proportion of studies including animals of both sexes from 2011-2021.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Many of the methods in this study were strong or adequate. Although the descriptive statistics appear solid, there are significant problems that need to be addressed in the selection and use of inferential statistics.

(1) One of the design elements that was studied was sample size estimation. This is usually done by a power analysis. The authors should consider what group size for the examined journals is adequate for their statistics to be valid. Or they could report the power of their studies to achieve a given meaningful difference.

We thank the reviewer for this excellent observation. We unfortunately failed to conduct an a priori power analysis. Previous research (Gupta, et al. 2016) suggests that post-hoc power calculations should not be carried out after the study has been conducted. We acknowledge the importance of establishing a sufficient sample size to draw sound conclusions based on an adequate effect size, and we regret that we did not carry out the appropriate estimations. We are very appreciative of the reviewer’s suggestions and aim to implement such an appropriate study design element in future studies.

Gupta KK, Attri JP, Singh A, Kaur H, Kaur G. Basic concepts for sample size calculation: Critical step for any clinical trials!. Saudi J Anaesth. 2016;10(3):328-331. doi:10.4103/1658-354X.174918

(2) A Bonferroni correction was used extensively. Because of its use, the corrected p values often appear much too high. The Bonferroni test becomes much too conservative for more than 3 or 4 tests. I suggest using a different test for multiple comparisons.

We thank the reviewer for their insightful suggestion. We have updated all p-values to reflect a Holm-Bonferroni correction instead. All p-values have been corrected and updated.

(3) The use of the chi-square test for categorical data is appropriate. However, the t-test and multiple regression tests are designed for continuous variables. Here, it appears that they were used for the nominal variables (Table 1). For these nominal data, other nonparametric tests should be used.

We thank the reviewer for this valuable insight. We have updated our statistical analysis methods and now use nonparametric Kruskal-Wallis tests to analyze differences in SDE reporting across journals, instead of chi-square test. Our reported p-values have been adjusted accordingly.

(4) It is not clear exactly when each test is used. The stats section in Methods should better delineate when each test is used. In addition, it would be helpful to include the test used in the figure legends.

We thank the reviewer for bringing up this important point. We have now updated the methods section to better delineate which tests were used, and also included the specific tests in the figure legends.

(5) You will need to rewrite some sections of the text to reflect the changes due to changing your use of statistics.

We have rewritten the sections of the text to reflect the changes in our use of statistics.

Here are a few comments on the presentation.

(1) Some of the figure legends are almost impossible to read. They are too congested.

We thank the reviewer for pointing this out. We have edited the figure legends to make them more readable. We will also attach a pdf with the graphs to allow for easier formatting.

(2) Also, is it possible to drop some of the panels in Figure 1?

The panels in figure 1 have been rearranged to make them more readable. We believe that each panel provides valuable visual summaries of our data, that will aid readers in understanding our results.

(3) It is not mandatory that values of y-axis on the graphs go up 100% (Figs 2 and 3). Using a maximum value of 100% clumps the lines visually. I suggest a max value on the y-axis of the graph of 50% or 60%. That will spread the lines better visually so differences can better be seen.

We thank the reviewer for considering the experience of our paper’s readers. The y-axes of Figures 2 and 3 have been truncated to 50%. The trend lines in each Figure now appear more separated and differences can better be seen.

Reviewer #2 (Recommendations For The Authors):

The authors did not use the exact same journals as they did in the 2017 study. This makes comparing the results complicated. Also, they pulled papers from 2011 to 2021, and hence cannot assess the impact of their own prior paper.

We appreciate the reviewer’s concern in maintaining consistency with the paper published by Ramirez, et al. in 2017. To clarify, our efforts focused on providing a replication study that expanded upon the original Ramirez publication - which we have no affiliation with. For our study, we used different academic journals than those used by Ramirez, et al, and also a different time-frame. We have updated the language in the manuscript to better-clarify the purpose and parameters of our study relative to the previous, unaffiliated, study.

The authors write "the proportion of studies including animals of both biological sexes generally increased between 2011 and 2021, though not significantly (R2= 0.0762, F(1,9)= 0.742, p= 0.411 (corrected p=8.2". This statement is not rigorous because the regression result is not statistically significant. Their data supports neither a claim of an increase nor a decrease over time. A similar problem repeats several times in the remainder of their results presentation.

Thank you for bringing this information to our attention. We agree with the concern regarding the statement, “the proportion of studies including animals of both biological sexes generally increased between 2011 and 2021, though not significantly (R2= 0.0762, F(1,9)= 0.742, p= 0.411 (corrected p=8.2.” We have rephrased the statement. Our updated Holm-Bonferroni corrected p-value is now noted in this more appropriately worded description of our results. Lastly, we have addressed the wording and redundancy seen in both the introduction and discussion and have made both more concise.

I think the Introduction and the Discussion are somewhat repetitive and the wording could be reduced.

We thank the reviewer for bringing this to our attention. We have addressed the redundancy across the Introduction and the Discussion. We have also altered the wording to reflect a more concise explanation of our study.

The 'trends' are not statistically significant. A non-significant trend does not exist and no claim of a 'trend' is justified by the data.

We thank the reviewer for this observation. We have updated the phrasing of ‘trends’ in all areas of the manuscript.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this paper Kawasaki et al describe a regulatory role for the PIWI/piRNA pathway in rRNA regulation in Zebrafish. This regulatory role was uncovered through a screen for gonadogenesis defective mutants, which identified a mutation in the meioc gene, a coiled-coil germ granule protein. Loss of this gene leads to redistribution of Piwil1 from germ granules to the nucleolus, resulting in silencing of rRNA transcription.

Strengths:

Most of the experimental data provided in this paper is compelling. It is clear that in the absence of meioc, PiwiL1 translocates in to the nucleolus and results in down regulation of rRNA transcription. the genetic compensation of meioc mutant phenotypes (both organismal and molecular) through reduction in PiwiL1 levels are evidence for a direct role for PiwiL1 in mediating the phenotypes of meioc mutant.

Weaknesses:

Questions remain on the mechanistic details by which PiwiL1 mediated rRNA down regulation, and whether this is a function of Piwi in an unperturbed/wildtype setting. There is certainly some evidence provided in support of the natural function for piwi in regulating rRNA transcription (figure 5A+5B). However, the de-enrichment of H3K9me3 in the heterozygous (Figure 6F) is very modest and in my opinion not convincingly different relative to the control provided. It is certainly possible that PiwiL1 is regulating levels through cleavage of nascent transcripts. Another aspect I found confounding here is the reduction in rRNA small RNAs in the meioc mutant; I would have assumed that the interaction of PiwiL1 with the rRNA is mediated through small RNAs but the reduction in numbers do not support this model. But perhaps it is simply a redistribution of small RNAs that is occurring. Finally, the ability to reduce PiwiL1 in the nucleolus through polI inhibition with actD and BMH-21 is surprising. What drives the accumulation of PiwiL1 in the nucleolus then if in the meioc mutant there is less transcription anyway?

Despite the weaknesses outlined, overall I find this paper to be solid and valuable, providing evidence for a consistent link between PIWI systems and ribosomal biogenesis. Their results are likely to be of interest to people in the community, and provide tools for further elucidating the reasons for this link.

The amount of cytoplasmic rRNA in piwi+/- was increased by 26% on average (figure 5A+5B), the amount of ChiP-qPCR of H3K9 was decreased by about 26% (Figure 6F), and ChiP-qPCR of Piwil1 was decreased by 35% (Figure 6G), so we don't think there is a big discrepancy. On the other hand, the amount of ChiP-qPCR of H3K9 in meioc^mo/mo was increased by about 130% (Figure 6F), while ChiP-qPCR of Piwil1 was increased by 50%, so there may be a mechanism for H3K9 regulation of Meioc that is not mediated by Piwil1. As for what drives the accumulation of Piwil1 in the nucleolus, although we have found that Piwil1 has affinity for rRNA (Fig. 6A), we do not know what recruits it. Significant increases in the 18-35nt small RNA of 18S, 28S rRNA and R2 were not detected in meioc^mo/mo testes enriched for 1-8 cell spermatogonia, compared with meioc^+/mo testes. The nucleolar localization of Piwil1 has revealed in this study, which will be a new topic for future research.

Reviewer #2 (Public review):

Summary:

In this study, the authors report that Meioc is required to upregulate rRNA transcription and promote differentiation of spermatogonial stem cells in zebrafish. The authors show that upregulated protein synthesis is required to support spermatogonial stem cells' differentiation into multi-celled cysts of spermatogonia. Coiled coil protein Meioc is required for this upregulated protein synthesis and for increasing rRNA transcription, such that the Meioc knockout accumulates 1-2 cell spermatogonia and fails to produce cysts with more than 8 spermatogonia. The Meioc knockout exhibits continued transcriptional repression of rDNA. Meioc interacts with and sequesters Piwil1 to the cytoplasm. Loss of Meioc increases Piwil1 localization to the nucleolus, where Piwil1 interacts with transcriptional silencers that repress rRNA transcription.

Strengths:

This is a fundamental study that expands our understanding of how ribosome biogenesis contributes to differentiation and demonstrates that zebrafish Meioc plays a role in this process during spermatogenesis. This work also expands our evolutionary understanding of Meioc and Ythdc2's molecular roles in germline differentiation. In mouse, the Meioc knockout phenocopies the Ythdc2 knockout, and studies thus far have indicated that Meioc and Ythdc2 act together to regulate germline differentiation. Here, in zebrafish, Meioc has acquired a Ythdc2-independent function. This study also identifies a new role for Piwil1 in directing transcriptional silencing of rDNA.

Weaknesses:

There are limited details on the stem cell-enriched hyperplastic testes used as a tool for mass spec experiments, and additional information is needed to fully evaluate the mass spec results. What mutation do these testes carry? Does this protein interact with Meioc in the wildtype testes? How could this mutation affect the results from the Meioc immunoprecipitation?

Stem cell-enriched hyperplastic testes came from wild-type adult sox17::GFP transgenic zebrafish. Sperm were found in these hyperplastic testes, and when stem cells were transplanted, they self-renewed and differentiated into sperm. It is not known if the hyperplasias develop due to a genetic variant in the line. We will add the following comment.

“The stem cell-enriched hyperplastic testes, which are occasionally found in adult wildtype zebrafish, contain cells at all stages of spermatogenesis. Hyperplasia-derived SSCs self-renewed and differentiated in the same manner as SSCs of normal testes in transplants of aggregates mixed with normal testicular cells.”

Reviewer #3 (Public review):

Summary:

The paper describes the molecular pathway to regulate germ cell differentiation in zebrafish through ribosomal RNA biogenesis. Meioc sequesters Piwil1, a Piwi homolog, which suppresses the transcription of the 45S pre-rDNA by the formation of heterochromatin, to the perinuclear bodies. The key results are solid and useful to researchers in the field of germ cell/meiosis as well as RNA biosynthesis and chromatin.

Strengths:

The authors nicely provided the molecular evidence on the antagonism of Meioc to Piwil1 in the rRNA synthesis, which supported by the genetic evidence that the inability of the meioc mutant to enter meiosis is suppressed by the piwil1 heterozygosity.

Weaknesses:

(1) Although the paper provides very convincing evidence for the authors' claim, the scientific contents are poorly written and incorrectly described. As a result, it is hard to read the text. Checking by scientific experts would be highly recommended. For example, on line 38, "the global translation activity is generally [inhibited]", is incorrect and, rather, a sentence like "the activity is lowered relative to other cells" is more appropriate here. See minor points for more examples.

Thank you for pointing that out. I will correct the parts pointed out.

(2) In some figures, it is hard for readers outside of zebrafish meiosis to evaluate the results without more explanation and drawing.

We will refine Figure 1A and add schema of spermatogonia culture system in a supplemental figure. 

(3) Figure 1E, F, cycloheximide experiments: Please mention the toxicity of the concentration of the drug in cell proliferation and viability.

When testicular tissue culture was performed at 0.1, 1, 10, 100, 250, and 500mM, abnormal strong OP-puro signals including nuclei were found in cells at 10mM or more. We will add the results in the Supplemental Material. In addition, at 1mM, growth was perturbed in fast-growing 32≤-cell cysts of spermatogonia, but not in 1-4-cell spermatogonia, as described in L122-125.

Author response:

Reviewer #1 (Public review):

Summary:

By way of background, the Jiang lab has previously shown that loss of the type II BMP receptor Punt (Put) from intestinal progenitors (ISCs and EBs) caused them to differentiate into EBs, with a concomitant loss of ISCs (Tian and Jiang, eLife 2014). The mechanism by which this occurs was activation of Notch in Put-deficient progenitors. How Notch was upregulated in Put-deficient ISCs was not established in this prior work. In the current study, the authors test whether a very low level of Dl was responsible. But co-depletion of Dl and Put led to a similar phenotype as depletion of Put alone. This result suggested that Dl was not the mechanism. They next investigate genetic interactions between BMP signaling and Numb, an inhibitor of Notch signaling. Prior work from Bardin, Schweisguth and other labs has shown that Numb is not required for ISC self-renewal. However the authors wanted to know whether loss of both the BMP signal transducer Mad and Numb would cause ISC loss. This result was observed for RNAi depletion from progenitors and for mad, numb double mutant clones. Of note, ISC loss was observed in 40% of mad, numb double mutant clones, whereas 60% of these clones had an ISC. They then employed a two-color tracing system called RGT to look at the outcome of ISC divisions (asymmetric (ISC/EB) or symmetric (ISC/ISC or EB/EB)). Control clones had 69%, 15% and 16%, respectively, whereas mad, numb double mutant clones had much lower ISC/ISC (11%) and much higher EB/EB (37%). They conclude that loss of Numb in moderate BMP loss of function mutants increased symmetric differentiation which lead caused ISC loss. They also reported that Numb¹⁵ and numb⁴ clones had a moderate but significant increase in ISC-lacking clones compared to control clones, supporting the model that Numb plays a role in ISC maintenance. Finally, they investigated the relevance of these observation during regeneration. After bleomycin treatment, there was a significant increase in ISC-lacking clones and a significant decrease in clone size in numb⁴ and Numb¹⁵ clones compared to control clones. Because bleomycin treatment has been shown to cause variation in BMP ligand production, the authors interpret the numb clone under bleomycin results as demonstrating an essential role of Numb in ISC maintenance during regeneration.

Strengths:

(i) Most data is quantified with statistical analysis

(ii) Experiments have appropriate controls and large numbers of samples

(iii) Results demonstrate an important role of Numb in maintaining ISC number during regeneration and a genetic interaction between Mad and Numb during homeostasis.

Weaknesses:

(i) No quantification for Fig. 1

Thank you for your suggestion. Quantification of Fig.1 will be added.  

(ii) The premise is a bit unclear. Under homeostasis, strong loss of BMP (Put) leads to loss of ISCs, presumably regardless of Numb level (which was not tested). But moderate loss of BMP (Mad) does not show ISC loss unless Numb is also reduced. I am confused as to why numb does not play a role in Put mutants. Did the authors test whether concomitant loss of Put and Numb leads to even more ISC loss than Put-mutation alone.

Thank you for your comment. We have tested the genetic interaction between punt and numb using punt RNAi and numb RNAi driven by esg^ts. According to the results in this study and our previously published data, punt mutant clone or esg^ts> punt RNAi could induce a rapid loss of ISC (whin 8 days). We did not observe further enhancement of stem cell loss phenotype caused punt RNAi by numb RNAi.

(iii) I think that the use of the word "essential" is a bit strong here. Numb plays an important role but in either during homeostasis or regeneration, most numb clones or mad, numb double mutant clones still have ISCs. Therefore, I think that the authors should temper their language about the role of Numb in ISC maintenance.

Thank you. We will revise the language.

Reviewer #2 (Public review):

Summary:

This work assesses the genetic interaction between the Bmp signaling pathway and the factor Numb, which can inhibit Notch signalling. It follows up on the previous studies of the group (Tian, Elife, 2014; Tian, PNAS, 2014) regarding BMP signaling in controlling stem cell fate decision as well as on the work of another group (Sallé, EMBO, 2017) that investigated the function of Numb on enteroendocrine fate in the midgut. This is an important study providing evidence of a Numb-mediated back up mechanism for stem cell maintenance.

Strengths:

(1) Experiments are consistent with these previous publications while also extending our understanding of how Numb functions in the ISC.

(2) Provides an interesting model of a "back up" protection mechanism for ISC maintenance.

Weaknesses:

(1) Aspects of the experiments could be better controlled or annotated:

(a) As they "randomly chose" the regions analyzed, it would be better to have all from a defined region (R4 or R2, for example) or to at least note the region as there are important regional differences for some aspects of midgut biology.

Thank you. Since we mainly focus on region 4, we have added the clarification in the manuscript.

(b) It is not clear to me why MARCM clones were induced and then flies grown at 18{degree sign}C? It would help to explain why they used this unconventional protocol.

To avoid spontaneous clone, we kept the flies under 18°C.

(2) There are technical limitations with trying to conclude from double-knockdown experiments in the ISC lineage, such as those in Figure 1 where Dl and put are both being knocked down: depending on how fast both proteins are depleted, it may be that only one of them (put, for example) is inactivated and affects the fate decision prior to the other one (Dl) being depleted. Therefore, it is difficult to definitively conclude that the decision is independent of Dl ligand.

In our hand, Dl-RNAi is very effective and exhibited loss of N pathway activity as determined by the N pathway reporter Su(H)-lacZ (Fig. 1D). Therefore, the ectopic Su(H)-lacZ expression in Punt Dl double RNAi (fig. 1E) is unlikely due to residual Dl expression. Nevertheless, we will change the statement “BMP signaling blocks ligand-independent N activity” to” Loss of BMP signaling results in ectopic N pathway activity even when Dl is depleted”

(3) Additional quantification of many phenotypes would be desired.

(a) It would be useful to see esg-GFP cells/total cells and not just field as the density might change (2E for example).

We focused on R4 region for quantification where the cell density did not exhibit apparent change in different experimental groups. In addition, we have examined many guts for quantification. It is unlikely that the difference in the esg+ cell number is caused by change in cell density.

(b) Similarly, for 2F and 2G, it would be nice to see the % of ISC/ total cell and EB/total cell and not only per esgGFP+ cell.

Unfortunately, we didn’t have the suggested quantification. However, we believe that quantification of the percentage of ISC or EB among all progenitor cells, as we did here, provides a faithful measurement of the self-renewal status of each experimental group.

(c) Fig1: There is no quantification - specifically it would be interesting to know how many esg+ are su(H)lacZ positive in Put- Dl- condition compared to WT or Put- alone. What is the n?

Quantification will be added.

(d) Fig2: Pros + cells are not seen in the image? Are they all DllacZ+?

Anti-Pros and anti-E(spl)mβ-CD2 were stained in the same channel (magenta).  Pros+ is nuclear dot-like staining, while CD2 outlined the cell membrane of EB cell.

(e) Fig3: it would be nice to have the size clone quantification instead of the distribution between groups of 2 cell 3 cells 4 cell clones.

Thank you for your suggestion. In this study, we have quantified the clone size of each clone and calculated the average size for each genotype. However, the frequency distribution analysis was chosen because it highlights the significance of the clone size differences among genotypes.

(f) How many times were experiments performed?

All experiments are performed 3 times.

(4) The authors do not comment on the reduction of clone size in DSS treatment in Figure 6K. How do they interpret this? Does it conflict with their model of Bleo vs DSS?

numb⁴ clone containing guts treated with DSS exhibited a slight reduction of clone size, evident by a higher percentage of 2-cell clones and lower percentage of > 8 cell clones. This reduction is less significant in guts containing numb¹⁵ clones. However, the percentage of Dl⁺-containing clones is similar between DSS and mock-treated guts. It is possible that ISC proliferation is lightly reduced due to numb⁴ mutation or the genetic background.

(5) There is probably a mistake on sentence line 314 -316 "Indeed, previous studies indicate that endogenous Numb was not undetectable by Numb antibodies that could detect Numb expression in the nervous system".

We will make a correction of the sentence.

Reviewer #3 (Public review):

Summary:

The authors provide an in-depth analysis of the function of Numb in adult Drosophila midgut. Based on RNAi combinations and double mutant clonal analyses, they propose that Numb has a function in inhibiting Notch pathway to maintain intestinal stem cells, and is a backup mechanism with BMP pathway in maintaining midgut stem cell mediated homeostasis.

Strengths:

Overall, this is a carefully constructed series of experiments, and the results and statistical analyses provides believable evidence that Numb has a role, albeit weak compared to other pathways, in sustaining ISC and in promoting regeneration especially after damage by bleomycin, which may damage enterocytes and therefore disrupt BMP pathway more. The results overall support their claim.

The data are highly coherent, and support a genetic function of Numb, in collaborating with BMP signaling, to maintain the number and proliferative function of ISCs in adult midguts. The authors used appropriate and sophisticated genetic tools of double RNAi, mutant clonal analysis and dual marker stem cell tracing approaches to ensure the results are reproducible and consistent. The statistical analyses provide confidence that the phenotypic changes are reliable albeit weaker than many other mutants previously studied.

Weaknesses:

In the absence of Numb itself, the midgut has a weak reduction of ISC number (Fig. 3 and 5), as well as weak albeit not statistically significant reduction of ISC clone size/proliferation. I think the authors published similar experiments with BMP pathway mutants. The mad^1-2 allele used here as stated below may not be very representative of other BMP pathway mutants. Therefore, it could be beneficial to compare the number of ISC number and clone sizes between other BMP experiments to provide the readers with a clearer picture of how these two pathways individually contribute (stronger/weaker effects) to the ISC number and gut homeostasis.

Thank you for your comment. We have tested other components of BMP pathway in our previously study (Tian et al., 2014). More complete loss of BMP signaling (for example, Put clones, Put RNAi, Tkv/Sax double mutant clones or double RNAi) resulted in ISC loss regardless of the status of numb, suggesting a more predominant role of BMP signaling in ISC self-renewal compared with Numb. We speculate that the weak stem cell loss phenotype associated with numb mutant clones in otherwise wild type background could be due to fluctuation of BMP signaling in homeostatic guts.

The main weakness of this manuscript is the analysis of the BMP pathway components, especially the mad^1-2 allele. The mad RNAi and mad^1-2 alleles (P insertion) are supposed to be weak alleles and that might be suitable for genetic enhancement assays here together with numb RNAi. However, the mad^1-2 allele, and sometimes the mad RNAi, showed weakly increased ISC clone size. This is kind of counter-intuitive that they should have a similar ISC loss and ISC clone size reduction.

We used mad^1-2 and mad RNAi here to test the genetic interaction with numb because our previous studies showed that partial loss of BMP signaling under these conditions did not cause stem cell loss, therefore, may provide a sensitized background to determine the role of Numb in ISC self-renewal. The increased proliferation of ISC/ clone size in associated with mad^1-2 and mad RNAi is due to the fact that the reduction of BMP signaling in either EC or EB will non-autonomously induce stem cell proliferation. However, in mad numb double mutant clones, there was a reduction in clone size, which correlated with loss of ISC.

A much stronger phenotype was observed when numb mutants were subject to treatment of tissue damaging agents Bleomycin, which causes damage in different ways than DSS. Bleomycin as previously shown to be causing mainly enterocyte damage,  and therefore disrupt BMP signaling from ECs more likely. Therefore, this treatment together with loss of numb led to a highly significant reduction of ISC in clones and reduction of clone size/proliferation. One improvement is that it is not clear whether the authors discussed the nature of the two numb mutant alleles used in this study and the comparison to the strength of the RNAi allele. Because the phenotypes are weak and more variable, the use of specific reagents is important.

Numb¹⁵ is a null allele, and the nature of numb⁴ has not been elucidated. According to Domingos, P.M. et al., numb¹⁵ induced a more severe phenotype than numb⁴ did. Consistently, we also found that more numb¹⁵ mutant clones were void of stem cell than numb⁴.

Furthermore, the use of possible activating alleles of either or both pathways to test genetic enhancement or synergistic activation will provide strong support for the claims.

Activation of BMP (Tkv^CA) also induced stem cell tumor (Tian et al., 2014), which is not suitable for synergistic activation experiment.

Author response:

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

eLife Assessment

This study offers a useful treatment of how the population of excitatory and inhibitory neurons integrates principles of energy efficiency in their coding strategies. The analysis provides a comprehensive characterisation of the model, highlighting the structured connectivity between excitatory and inhibitory neurons. However, the manuscript provides an incomplete motivation for parameter choices. Furthermore, the work is insufficiently contextualized within the literature, and some of the findings appear overlapping and incremental given previous work.

We are genuinely grateful to the Editors and Reviewers for taking time to provide extremely valuable suggestions and comments, which will help us to substantially improve our paper. We decided to do our very best to implement all suggestions, as detailed in the point-by-point rebuttal letter below. We feel that our paper has improved considerably as a result. 

Public Reviews:

Reviewer #1 (Public Review): 

Summary: Koren et al. derive and analyse a spiking network model optimised to represent external signals using the minimum number of spikes. Unlike most prior work using a similar setup, the network includes separate populations of excitatory and inhibitory neurons. The authors show that the optimised connectivity has a like-to-like structure, leading to the experimentally observed phenomenon of feature competition. They also characterise the impact of various (hyper)parameters, such as adaptation timescale, ratio of excitatory to inhibitory cells, regularisation strength, and background current. These results add useful biological realism to a particular model of efficient coding. However, not all claims seem fully supported by the evidence. Specifically, several biological features, such as the ratio of excitatory to inhibitory neurons, which the authors claim to explain through efficient coding, might be contingent on arbitrary modelling choices. In addition, earlier work has already established the importance of structured connectivity for feature competition. A clearer presentation of modelling choices, limitations, and prior work could improve the manuscript.

Thanks for these insights and for this summary of our work.  

Major comments:

(1) Much is made of the 4:1 ratio between excitatory and inhibitory neurons, which the authors claim to explain through efficient coding. I see two issues with this conclusion: (i) The 4:1 ratio is specific to rodents; humans have an approximate 2:1 ratio (see Fang & Xia et al., Science 2022 and references therein); (ii) the optimal ratio in the model depends on a seemingly arbitrary choice of hyperparameters, particularly the weighting of encoding error versus metabolic cost. This second concern applies to several other results, including the strength of inhibitory versus excitatory synapses. While the model can, therefore, be made consistent with biological data, this requires auxiliary assumptions.

We now describe better the ratio of numbers of E and I neurons found in real data, as suggested. The first submission already contained an analysis of how the optimal ratio of E vs I neuron numbers depends in our model on the relative weighting of the loss of E and I neurons and on the relative weighting of the encoding error vs the metabolic cost in the loss function (see Fig. 7E). We revised the text on page 12 describing Fig. 7E. 

To allow readers to form easily a clear idea of how the weighting of the error vs the cost may influence the optimal network configuration, we now present how optimal parameters depend on the weighting in a systematic way, by always including this type of analysis when studying all other model parameters (time constants of single E and I neurons, noise intensity, metabolic constant, ratio of mean I-I to E-I connectivity). These results are shown on the Supplementary Fig. S4 A-D and H, and we comment briefly on each of them in Results sections (pages 9, 10, 11 and 12) that analyze each of these parameters.  

Following this Reviewer’s comment, we now included a joint analysis of network performance relative to the ratio of E-I neuron numbers and the ratio of mean I-I to E-I connectivity (Fig. 7J). We found a positive correlation between optima values of these two ratios. This implies that a lower ratio of E-I neuron numbers, such as a 2:1 ratio in human cortex mentioned by the reviewer, predicts lower optimal ratio of I-I to E-I connectivity and thus weaker inhibition in the network. We made sure that this finding is suitably described in revision (page 13).

(2) A growing body of evidence supports the importance of structured E-I and I-E connectivity for feature selectivity and response to perturbations. For example, this is a major conclusion from the Oldenburg paper (reference 62 in the manuscript), which includes extensive modelling work. Similar conclusions can be found in work from Znamenskiy and colleagues (experiments and spiking network model; bioRxiv 2018, Neuron 2023 (ref. 82)), Sadeh & Clopath (rate network; eLife, 2020), and Mackwood et al. (rate network with plasticity; eLife, 2021). The current manuscript adds to this evidence by showing that (a particular implementation of) efficient coding in spiking networks leads to structured connectivity. The fact that this structured connectivity then explains perturbation responses is, in the light of earlier findings, not new.

We agree that the main contribution of our manuscript in this respect is to show how efficient coding in spiking networks can lead to structured connectivity implementing lateral inhibition similar to that proposed in the recent studies mentioned by the Reviewer. We apologize if this was not clear enough in the previous version. We streamlined the presentation to make it clearer in revision.  We nevertheless think it useful to report the effects of perturbations within this network because these results give information about how lateral inhibition works in our network. Thus, we kept presenting it in the revised version, although we de-emphasized and simplified its presentation. We now give more emphasis to the novelty of the derivation of this connectivity rule from the principles of efficient coding (pages 4 and 6). We also describe better (page 8) what the specific results of our simulated perturbation experiments add to the existing literature.

(3) The model's limitations are hard to discern, being relegated to the manuscript's last and rather equivocal paragraph. For instance, the lack of recurrent excitation, crucial in neural dynamics and computation, likely influences the results: neuronal time constants must be as large as the target readout (Figure 4), presumably because the network cannot integrate the signal without recurrent excitation. However, this and other results are not presented in tandem with relevant caveats.

We improved the Limitations paragraph in Discussion, and also anticipated caveats in tandem with results when needed, as suggested. 

We now mention the assumption of equal time constants between the targets and readouts in the Abstract. 

We now added the analysis of the network performance and dynamics as a function of the time constant of the target (t_x) to the Supplementary Fig S5 (C-E). These results are briefly discussed in text on page 13. The only measure sensitive to t_x is the encoding error of E neurons, with a minimum at t_x =9 ms, while I neurons and metabolic cost show no dependency. Firing rates, variability of spiking as well as the average and instantaneous balance show no dependency on t_x. We note that t_x = t, with t=1/l the time constant of the population readout (Eq. 9), is an assumption we use when we derive the model from the efficiency objective (Eq. 18 to 23). In our new and preliminary work (Koren, Emanuel, Panzeri, Biorxiv 2024), we derived a more general class of models where this assumption is relaxed, which gives a network with E-E connectivity that adapts to the time constant of the stimulus. Thus, the reviewer is correct in the intuition that the network requires E-E connectivity to better integrate target signals with a different time constant than the time constant of the membrane. We now better emphasize this limitation in Discussion (page 16).

(4) On repeated occasions, results from the model are referred to as predictions claimed to match the data. A prediction is a statement about what will happen in the future – but most of the “predictions” from the model are actually findings that broadly match earlier experimental results, making them “postdictions”.

This distinction is important: compared to postdictions, predictions are a much stronger test because they are falsifiable. This is especially relevant given (my impression) that key parameters of the model were tweaked to match the data.

We now comment on every result from the model as either matching earlier experimental results, or being a prediction for experiments. 

In Section “Assumptions and emergent properties of the efficient E-I network derived from first principles”, we report (page 4) that neural networks have connectivity structure that relates to tuning similarity of neurons (postdiction). 

In Section “Encoding performance and neural dynamics in an optimally efficient E-I network” we report (page 5) that in a network with optimal parameters, I neurons have higher firing rate than E neurons (postdiction), that single neurons show temporally correlated synaptic currents (postdiction) and that the distribution of firing rates across neurons is log-normal (postdiction). 

In Section “Competition across neurons with similar stimulus tuning emerging in efficient spiking networks” we report (page 6)  that the activity perturbation of E neurons induces lateral inhibition on other E neurons, and that the strength of lateral inhibition depends on tuning similarity (postdiction). We show that activity perturbation of E neurons induces lateral excitation in I neurons (prediction). We moreover show that the specific effects of the perturbation of neural activity rely on structured E-I-E connectivity (prediction for experiments, but similar result in Sadeh and Clopath, 2020). We show strong voltage correlations but weak spike-timing correlations in our network (prediction for experiments, but similar result in Boerlin et al. 2013). 

In Section “The effect of structured connectivity on coding efficiency and neural dynamics”, we report (page 7) that our model predicts a number of differences between networks with structured and unstructured (random) connectivity. In particular, structured networks differ from unstructured ones by showing better encoding performance, lower metabolic cost, weaker variance over time in the membrane potential of each neuron, lower firing rates and weaker average and instantaneous balance of synaptic currents.

In Section “Weak or no spike-triggered adaptation optimizes network efficiency”, we report (page 9) that our model predicts better encoding performance in networks with adaptation compared to facilitation. Our results suggest that adaptation should be stronger in E compared to I (PV+) neurons (postdiction). In the same section, we report (page 10) that our results suggest that the instantaneous balance is a better predictor of model efficiency than average balance (prediction).

In Section “Non-specific currents regulate network coding properties”, we report (page 10) that our model predicts that more than half of the distance between the resting potential and firing threshold is taken by external currents that are unrelated to feedforward processing (postdiction). We also report (page 11) that our model predicts that moderate levels of uncorrelated (additive) noise is beneficial for efficiency (prediction for experiments, but similar results in Chalk et al., 2016, Koren et al., 2017, Timcheck et al. 2022).

In Section “Optimal ratio of E-I neuron numbers and of mean I-I to E-I synaptic efficacy coincide with biophysical measurements”, we predict the optimal ratio of E to I neuron numbers to be 4:1 (postdiction) and the optimal ratio of mean I-I to E-I connectivity to be 3:1 (postdiction). Further, we report (page 13) that our results predict that a decrease in the ratio of E-I neuron numbers is accompanied with the decrease in the ratio of mean I-I to E-I connectivity. 

Finally, in Section “Dependence of efficient coding and neural dynamics on the stimulus statistics”, we report (page 13) that our model predicts that the efficiency of the network has almost no dependence on the time scale of the stimulus (prediction). 

Reviewer #2 (Public Review):

Summary:

In this work, the authors present a biologically plausible, efficient E-I spiking network model and study various aspects of the model and its relation to experimental observations. This includes a derivation of the network into two (E-I) populations, the study of single-neuron perturbations and lateral-inhibition, the study of the effects of adaptation and metabolic cost, and considerations of optimal parameters. From this, they conclude that their work puts forth a plausible implementation of efficient coding that matches several experimental findings, including feature-specific inhibition, tight instantaneous balance, a 4 to 1 ratio of excitatory to inhibitory neurons, and a 3 to 1 ratio of I-I to E-I connectivity strength. It thus argues that some of these observations may come as a direct consequence of efficient coding.

Strengths:

While many network implementations of efficient coding have been developed, such normative models are often abstract and lacking sufficient detail to compare directly to experiments. The intention of this work to produce a more plausible and efficient spiking model and compare it with experimental data is important and necessary in order to test these models.

In rigorously deriving the model with real physical units, this work maps efficient spiking networks onto other more classical biophysical spiking neuron models. It also attempts to compare the model to recent single-neuron perturbation experiments, as well as some longstanding puzzles about neural circuits, such as the presence of separate excitatory and inhibitory neurons, the ratio of excitatory to inhibitory neurons, and E/I balance. One of the primary goals of this paper, to determine if these are merely biological constraints or come from some normative efficient coding objective, is also important.

Though several of the observations have been reported and studied before (see below), this work arguably studies them in more depth, which could be useful for comparing more directly to experiments.

Thanks for these insights and for the kind words of appreciation of the strengths of our work.  

Weaknesses:

Though the text of the paper may suggest otherwise, many of the modeling choices and observations found in the paper have been introduced in previous work on efficient spiking models, thereby making this work somewhat repetitive and incremental at times. This includes the derivation of the network into separate excitatory and inhibitory populations, discussion of physical units, comparison of voltage versus spike-timing correlations, and instantaneous E/I balance, all of which can be found in one of the first efficient spiking network papers (Boerlin et al. 2013), as well as in subsequent papers. Metabolic cost and slow adaptation currents were also presented in a previous study (Gutierrez & Deneve 2019). Though it is perfectly fine and reasonable to build upon these previous studies, the language of the text gives them insufficient credit.

We indeed built our work on these important previous studies, and we apologize if this was not clear enough. We thus improved the text to make sure that credit to previous studies is more precisely and more clearly given (see detailed reply for the list of changes made). 

To facilitate the understanding on how we built on previous work, we expanded the comparison of our results with the results of Boerlin et al. (2013) about voltage correlations and uncorrelated spiking (page 7), comparison with the derivation of physical units of Boerlin et al. (2013) (page 3), discussion of how results on the ratio of the number of E to I neurons relate  to Calaim et al (2022) and Barrett et al. (2016) (page 16), and comment on the previous work by Gutierrez and Deneve about adaptation (page 8).  

Furthermore, the paper makes several claims of optimality that are not convincing enough, as they are only verified by a limited parameter sweep of single parameters at a time, are unintuitive and may be in conflict with previous findings of efficient spiking networks. This includes the following. 

Coding error (RMSE) has a minimum at intermediate metabolic cost (Figure 5B), despite the fact that intuitively, zero metabolic cost would indicate that the network is solely minimizing coding error and that previous work has suggested that additional costs bias the output. 

Coding error also appears to have a minimum at intermediate values of the ratio of E to I neurons (effectively the number of I neurons) and the number of encoded variables (Figures 6D, 7B). These both have to do with the redundancy in the network (number of neurons for each encoded variable), and previous work suggests that networks can code for arbitrary numbers of variables provided the redundancy is high enough (e.g., Calaim et al. 2022). 

Lastly, the performance of the E-I variant of the network is shown to be better than that of a single cell type (1CT: Figure 7C, D). Given that the E-I network is performing a similar computation as to the 1CT model but with more neurons (i.e., instead of an E neuron directly providing lateral inhibition to its neighbor, it goes through an interneuron), this is unintuitive and again not supported by previous work. These may be valid emergent properties of the E-I spiking network derived here, but their presentation and description are not sufficient to determine this.

With regard to the concern that our previous analyses considered optimal parameter sets determined with a sweep of a single parameter at a time, we have addressed this issue in two ways. First, we presented (Figure 6I and 7J and text on pages 11 and 13) results of joint sweeps of variations of pairs of parameters whose joint variations are expected to influence optimality in a way that cannot be understood varying one parameter at a time. These new analyses complement the joint parameter sweep of the time constants of single E and I neurons (t_r^E and t_r^I) that has already been presented in Fig. 5A (former Fig. 4A). Second, we conducted, within a reasonable/realistic range of possible variations of each individual parameter, a Monte-Carlo random joint sampling (10000 simulations with 20 trials each) of all 6 model parameters that we explored in the paper. We presented these new results on Fig. 2 and discuss it on pages 5-6. 

The Reviewer is correct in stating that the error (RMSE) exhibits a counterintuitive minimum as a function of the metabolic constant despite the fact that, intuitively, for vanishing metabolic constant the network is solely minimizing the coding error (Fig. 6B). In our understanding, this counterintuitive finding is due to the presence of noise in the membrane potential dynamics. In the presence of noise, a non-vanishing metabolic constant is needed to suppress “inefficient” spikes purely induced by noise that do not contribute to coding and increase the error. This gives rise to a form of “stochastic resonance”, where the noise improves detection of the signal coming from the feedforward currents. We note that the metabolic constant and the noise variance both appear in the non-specific external current (Eq. 29f in Methods), and, thus, a covariation in their optimal values is expected. Indeed, we find that the optimal metabolic constant monotonically increases as a function of the noise variance, with stronger regularization (larger beta) required to compensate for larger variability (larger sigma) (Fig. 6I). Finally, we note that a moderate level of noise (which, in turn, induces a non-trivial minimum of the coding error as a function of beta) in the network is optimal. The beneficial effect of moderate levels of noise on performance in networks with efficient coding has been shown in different contexts in previous work (Chalk et al. 2016, Koren and Deneve, 2017). The intuition is that the noise prevents the excessive synchronization of the network and insufficient single neuron variability that decrease the performance. The points above are now explained in the revised text on page 11.

The Reviewer is also correct in stating that the network exhibits an optimal performance for intermediate values of the number of I neurons and the number of encoded features. In our understanding, the optimal number of encoded features of M=3 arises simply because all the other parameters were optimized for those values of M. The purpose of those analyses was not to state that a network optimally encodes only a given number of features, but how a network whose parameters are optimized for a given M perform reasonably well when M is varied. We clarify this on page 13 of Results in Discussion on page 16. In the same Discussion paragraph we refer also to the results of Calaim et al mentioned by the Reviewer. 

To address the concern about the comparison of efficiency between the E-I and the 1CT model, we took advantage of the Reviewer’s suggestions to consider this issue more deeply. In revision, we now compare the efficiency of the 1CT model with the E population of the E-I model (Fig. 8H). This new comparison changes the conclusion about which model is more efficient, as it shows the 1CT model is slightly more efficient than the E-I model. Nevertheless, the E-I model performance is more robust to small variations of optimal parameters, e.g., it exhibits biologically plausible firing rates for non-optimal values of the metabolic constant. See also the reply to point 3 of the Public Review of Reviewer 2 for more detail. We added these results and the ensuing caveats for the interpretation of this comparison on Page 14, and also revised the title of the last subsection of Results.  

Alternatively, the methodology of the model suggests that ad hoc modeling choices may be playing a role. For example, an arbitrary weighting of coding error and metabolic cost of 0.7 to 0.3, respectively, is chosen without mention of how this affects the results. Furthermore, the scaling of synaptic weights appears to be controlled separately for each connection type in the network (Table 1), despite the fact that some of these quantities are likely linked in the optimal network derivation. Finally, the optimal threshold and metabolic constants are an order of magnitude larger than the synaptic weights (Table 1). All of these considerations suggest one of the following two possibilities. One, the model has a substantial number of unconstrained parameters to tune, in which case more parameter sweeps would be necessary to definitively make claims of optimality. Or two, parameters are being decoupled from those constrained by the optimal derivation, and the optima simply corresponds to the values that should come out of the derivation.

We thank the reviewer for bringing about these important questions.

In the first submission, we presented both the encoding error and the metabolic cost separately as a function of the parameters, so that readers could get an understanding of how stable optimal parameters would be to the change of the relative weighting of encoding error and metabolic cost. We specified this in Results (page 5) and we kept presenting separately encoding and metabolic terms in the revision.

However, we agree that it is important to present the explicit quantification on how the optimal parameters may depend on g_L. In the first submission, we showed the analysis for all possible weightings in case of two parameters for which we found this analysis was the most relevant – the ratio of neuron numbers (Fig. 7E, Fig. 6E in first submission) and the optimal number of input features M (see last paragraph on page 13 and Fig. 8D). We now show this analysis also for the rest of studied model parameters in the Supplementary Fig. S4 (A-D and H). This is discussed on pages 9, 10,11 and 12.

With regard to the concern that the scaling of synaptic weights should not be controlled separately for each connection type in the network, we agree and we would like to clarify that we did not control such scaling separately. Apologies if this was not clear enough. From the optimal analytical solution, we obtained that the connectivity scales with the standard deviation of decoding weights (s_w^E and s_w^I) of the pre and postsynaptic populations (Methods, Eq. 32). We studied the network properties as a function of the ratio of average I-I to E-I connectivity (Fig. 7 F-I; Supplementary Fig. S4 D-H), which is equivalent to the ratio of standard deviations s_w^I /s_w^E (see Methods, Eq. 35). We clarified this in text on page 12.

Next, it is correct that our synaptic weights are an order of magnitude smaller than the metabolic constant. We analysed a simpler version of the network that has the coding and dynamics identical to our full model (Methods, Eq. 25) but without the external currents. We found that the optimal parameters determining the firing threshold in such a simpler network were biologically implausible (see Supplementary Text 2 and Supplementary Table S1). We considered as another simple solution the rescaling of the synaptic efficacy such as to have biologically plausible threshold. However, that gave implausible mean synaptic efficacy (see Supplementary Text 2).  Thus, to be able to define a network with biologically plausible firing threshold and mean synaptic efficacy, we introduced the non-specific external current. After introducing such current, we were able to shift the firing threshold to biologically plausible values while keeping realistic values of mean synaptic efficacy. Biologically plausible values for the firing threshold are around 15 -– 20 mV above the resting potential (Constantinople and Bruno, 2013), which is the value that we have in our model. A plausible value for the average synaptic strength is between a fraction of one millivolt to a couple of millivolts (Constantinople & Bruno, 2013, Campagnola et al. 2022), which also corresponds to values that the synaptic weights take. The above results are briefly explained in the revised text on page 4.

Finally, to study the optimality of the network when changing multiple parameters at a time, we added a new analysis with Monte-Carlo random joint sampling (10.000 parameter sets with 20 trials for each set) of all 6 model parameters that we explored in the paper. We compared (Fig 2) the so-obtained results of each simulation with those obtained from the understanding gained from varying one or two parameters at a time (optimal parameters reported in Table 1 and used throughout the paper).  We found (Fig. 2) that the optimal configuration in Table 1 was never improved by any other simulations we performed, and that the first three random simulations that came the closest to the optimal one of Table 1 had stronger noise intensity but also stronger metabolic cost than the configuration on Table 1. The second, third and fourth configurations had longer time constants of both E and I single neurons (adaptation time constants). Ratio of E-I neuron numbers and of I-I to E-I connectivity in the second, third and fourth best configuration were either jointly increased or decreased with respect to our configuration. These results are reported on Fig. 2 and in Tables 2-3 and they are discussed in Results (page 5).

Reviewer #3 (Public Review):

Summary:

In their paper the authors tackle three things at once in a theoretical model: how can spiking neural networks perform efficient coding, how can such networks limit the energy use at the same time, and how can this be done in a more biologically realistic way than previous work?

They start by working from a long-running theory on how networks operating in a precisely balanced state can perform efficient coding. First, they assume split networks of excitatory (E) and inhibitory (I) neurons. The E neurons have the task to represent some lower dimensional input signal, and the I neurons have the task to represent the signal represented by the E neurons. Additionally, the E and I populations should minimize an energy cost represented by the sum of all spikes. All this results in two loss functions for the E and I populations, and the networks are then derived by assuming E and I neurons should only spike if this improves their respective loss. This results in networks of spiking neurons that live in a balanced state, and can accurately represent the network inputs.

They then investigate in-depth different aspects of the resulting networks, such as responses to perturbations, the effect of following Dale's law, spiking statistics, the excitation (E)/inhibition (I) balance, optimal E/I cell ratios, and others. Overall, they expand on previous work by taking a more biological angle on the theory and showing the networks can operate in a biologically realistic regime.

Strengths:

(1) The authors take a much more biological angle on the efficient spiking networks theory than previous work, which is an essential contribution to the field.

(2) They make a very extensive investigation of many aspects of the network in this context, and do so thoroughly.

(3) They put sensible constraints on their networks, while still maintaining the good properties these networks should have.

Thanks for this summary and for these kind words of appreciation of the strengths of our work.  

Weaknesses:

(1) The paper has somewhat overstated the significance of their theoretical contributions, and should make much clearer what aspects of the derivations are novel. Large parts were done in very similar ways in previous papers. Specifically: the split into E and I neurons was also done in Boerlin et al (2008) and in Barrett et al (2016). Defining the networks in terms of realistic units was already done by Boerlin et al (2008). It would also be worth it to discuss Barrett et al (2016) specifically more, as there they also use split E/I networks and perform biologically relevant experiments.

We improved the text to make sure that credit to previous studies is more precisely and more clearly given (see rebuttal to the specific suggestions of Reviewer 2 for a full list).

We apologize if this was not clear enough in the previous version. 

With regard to the specific point raised here about the E-I split, we revised the text on page 2. With regard to the realistic units, we revised the text on page 3. Finally, we commented on relation between our results and results of the study by Barrett et al. (2016) on page 16.

(2) It is not clear from an optimization perspective why the split into E and I neurons and following Dale's law would be beneficial. While the constraints of Dale's law are sensible (splitting the population in E and I neurons, and removing any non-Dalian connection), they are imposed from biology and not from any coding principles. A discussion of how this could be done would be much appreciated, and in the main text, this should be made clear.

We indeed removed non-Dalian connections because Dale’s law is a major constraint for biological plausibility. Our logic was to consider efficient coding within the space of networks that satisfy this (and other) biological plausibility constraints. We did not intend to claim that removing the non-Dalian connections was the result of an analytical optimization. We clarified this in revision (page 4).

(3) Related to the previous point, the claim that the network with split E and I neurons has a lower average loss than a 1 cell-type (1-CT) network seems incorrect to me. Only the E population coding error should be compared to the 1-CT network loss, or the sum of the E and I populations (not their average). In my author recommendations, I go more in-depth on this point.

We carefully considered these possibilities and decided to compare only the E population of the E-I model with the 1-CT model. On Fig.8G (7C of the first submission), E neurons have a slightly higher error and cost compared to the 1CT network. In the revision, we compared the loss of E neurons of the E-I model with the loss of the 1-CT model. Using such comparison, we found that the 1CT network has lower loss and is more efficient compared to E neurons of the E-I model. We revised Figure 8H and text on page 14 to address this point. 

(4) While the paper is supposed to bring the balanced spiking networks they consider in a more experimentally relevant context, for experimental audiences I don't think it is easy to follow how the model works, and I recommend reworking both the main text and methods to improve on that aspect.

We tried to make the presentation of the model more accessible to a non-computational audience in the revised paper. We carefully edited the text throughout to make it as accessible as possible. 

Assessment and context:

Overall, although much of the underlying theory is not necessarily new, the work provides an important addition to the field. The authors succeeded well in their goal of making the networks more biologically realistic, and incorporating aspects of energy efficiency. For computational neuroscientists, this paper is a good example of how to build models that link well to experimental knowledge and constraints, while still being computationally and mathematically tractable. For experimental readers, the model provides a clearer link between efficient coding spiking networks to known experimental constraints and provides a few predictions.

Thanks for these kind words. We revised the paper to make sure that these points emerge more clearly and in a more accessible way from the revised paper.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Referring to the major comments:

(1) Be upfront about particular modelling choices and why you made them; avoid talk of a "striking/surprising", etc. ability to explain data when this actually requires otherwise-arbitrary choices and auxiliary assumptions. Ideally, this nuance is already clear from the abstract.

We removed all the "striking/surprising" and similar expressions from the text. 

We added to the Abstract the assumption of equal time constants of the stimulus and of the membrane of E and I neurons and the assumption of the independence of encoded stimulus features.

In revision, we performed additional analyses (joint parameter sweeps, Monte-Carlo joint sampling of all 6 model parameters) providing additional evidence that the network parameters in Table 1 capture reasonably well the optimal solution. These are reported on Figs. 2, 6I and 7J and in Results (pages 5, 11 and 13). See rebuttal to weaknesses of the public review of the Referee 2 for details.

(2) Make even more of an effort to acknowledge prior work on the importance of structured E-I and I-E connectivity.

We have revised the text (page 4) to better place our results within previous work on structured E-I and I-E connectivity.

(3) Be clear about the model's limitations and mention them throughout the text. This will allow readers to interpret your results appropriately.

We now comment more on model's limitations, in particular the simplifying assumption about the network's computation (page 16), the lack of E-E connectivity (page 3), the absence of long-term adaptation (page 10), and the simplification of only having one type of inhibitory neurons (page 16). 

(4) Present your "predictions" for what they are: aspects of the model that can be made consistent with the existing data after some fitting. Except in the few cases where you make actual predictions, which deserve to be highlighted.

We followed the suggestion of the reviewer and distinguished cases where the model is consistent with the data (postdictions) from actual predictions, where empirical measurements are not available or not conclusive. We compiled a list of predictions and postdictions in response to the point 4 of Reviewer 1. In revision, we now comment about every property of the model as either reproducing a known property of biological networks (postdiction) or being a prediction. We improved the text in Results on pages 4, 5, 6, 7, 9, 10, 11, 12 and 13 to accommodate these requests.

Minor comments and recommendations

It's a sizable list, but most can be addressed with some text edits.

(1) The image captions should give more details about the simulations and analyses, particularly regarding sample sizes and statistical tests. In Figure 5, for example, it is unclear if the lines represent averages over multiple signals and, if so, how many. It's probably not a single realization, but if it is, this might explain the otherwise puzzling optimal number of three stimuli. Box plots visualize the distribution across simulation trials, but it's not clear how many. In Figure 7d, a star suggests statistical significance, but the caption does not mention the test or its results; the y-axis should also have larger limits.

All statistical results were computed on 100 or 200 simulation trials, depending on the figure, with duration of the trial of 1 second of simulated time. To compute statistical results in Fig. 1, we used 10 trials with duration of 10 seconds for each trial. Each trial consisted of M independent realizations of Ornstein-Uhlenbeck (OU) processes as stimuli, independent noise in the membrane potential and an independent draw of tuning parameters, such that the results are general over specific realization of these random variables. Realizations of the OU processes were independent across stimulus dimensions and across trials. We added this information in the caption of each figure. 

The optimal number of M=3 stimuli is the result of measuring the performance of the network in 100 simulation trials (for each parameter value), thus following the same procedure as for all other parameters. Boxplots on Fig. 8G-H were also generated from results computed in 100 simulation trials, which we have now specified in the caption of the figure, together with the statistical test used for assessing the significance (twotailed t-test). We also enlarged the limits of Fig. 8H (7D in the previous version).

(2) The Oldenburg paper (reference 62) finds suppression of all but nearby neurons in response to two- photon stimulation of small neural ensembles (instead of single neurons, as in Chettih & Harvey). This isn't perfectly consistent with the model's results, even though the Oldenburg experiments seem more relevant given the model's small size, and strong connectivity/high connection probability between similarly tuned neurons. What might explain the potential mismatch?

We sincerely apologize for not having been precise enough on this point when comparing our model against Chettih & Harvey and Oldenburg et al. We corrected the sentence (page 6) to remove the claim that our model reproduces both. 

We speculate that the discrepancy between perturbing our model and the Oldenburg data may arise from the lack of E-E connectivity in our model. Synaptic connections between E neurons with similar selectivity could create an enhancement instead of suppression between neuronal pairs with very similar tuning. We added a sentence about this in the section with perturbation experiments “Competition across neurons with similar stimulus tuning emerging in efficient spiking networks” (page 7) where we discuss this limitation of our model. We feel that this example shows the utility to derive some perturbation results from our model, as not all networks with some degree of lateral inhibition will show the same perturbation results. Comparing our model's perturbation with real data perturbation results has thus some value to better appreciate strengths and limitations of our approach. 

(3) "Previous studies optogenetically stimulated E neurons but did not determine whether the recorded neurons were excitatory or inhibitory " (p. 11). I believe Oldenburg et al. did specifically image excitatory neurons.

The reviewer is correct about Oldenburg et al. imaging specifically excitatory neurons. We have revised this part of the Discussion (page 15). 

(4) The authors write that efficiency is particularly achieved where adaptation is stronger in E compared to I neurons (p. 7; Figure 4). Although this would be consistent with experimental data (the I neurons in the model seem akin to fast-spiking Pv+ cells), I struggle to see it in the figure. Instead, it seems like there are roughly two regimes. If either of the neuronal timescales is faster than the stimulus timescale, the optimisation fails. If both are at least as slow, optimisation succeeds.

We agree with the reviewer that the adaptation properties of our inhibitory neurons are compatible with Pv+ cells. What is essential for determining the dynamical regime of the network is less the relation to the time constant of the stimulus (t_x) but rather the relation between the time constant of the population readout (t, which is also the membrane time constant) and the time constant of the single neuron (t_r^y for y=E and y=I; see Eq. 23, 25 or 29e). The relation between t and t_r^y determines if single neurons generate spike-triggered adaptation (t_r^y > t) or spike-triggered facilitation (t_r^y < t; see Table 4). In regimes with facilitation in either E or I neurons (or both), the network performance strongly deteriorates compared to regimes with adaptation (Fig. 5A). 

Beyond adaptation leading to better performance, we also found different effects of adaptation in E and I neurons. We acknowledge that the difference of these effects was difficult to see from the Fig. 4B in the first submission. We have now replotted results from previously shown Fig. 4B to focus on the adaptation regime only, (since the Fig. 5A already establishes that this is the regime with better performance). We also added figures showing the differential effect of adaptation in E and I cell type on the firing rate and on the average loss (Fig. 5C-D). Fig. 5B and C (top plots) show that with adaptation in E neurons, the error and the loss increase more slowly than with adaptation in I neurons. Moreover, the firing rate in both cell types decreases with adaptation in E neurons, while this is not the case with adaptation in I neurons (Fig. 5D). These results are added to the figure panels specified above and discussed in text on page 9.

To clarify the relation between neuronal and stimulus timescale, we now also added the analysis of network performance as a function of the time constant of the stimulus t_x (Supplementary Fig. S5 C-E). We found that the model's performance is optimal when the time constant of the stimulus is close to the membrane time constant t. This result is expected, because the equality of these time constants was imposed in our analytical derivation of the model (t_x  = t). We see a similar decrease in performance for values of t_x  that are faster and slower with respect to the membrane time constant (Supplementary Fig. S5C, top). These results are added to the figure panels specified above and discussed in text on page 13.

(5) A key functional property of cortical interneurons is their lower stimulus selectivity. Does the model replicate this feature?

We think that whether I neurons are less selective than E neurons is still an open question. A number of recent empirical studies reported that the selectivity of I neurons is comparable to the selectivity of E neurons (see., e.g., Kuan et al. Nature 2024, Runyan et al. Neuron 2010, Najafi et al. Neuron 2020). In our model, the optimal solution prescribes a precise structure in recurrent connectivity (see Eq. 24 and Fig. 1C(ii)) and structured connectivity endows I neurons with stimulus selectivity. To show this, we added plots of example tuning curves and the distribution of the selectivity index across E and I neurons (Fig. 8E-F) and described these new results in Results (page 14). Tuning curves in our network were similar to those computed in a previous work that addressed stimulus tuning in efficient spiking networks (Barrett et al. 2016). We evaluated tuning curves using M=3 constant stimulus features and we varied one of the features while the two others were kept fixed. We provided details on how the tuning curves and the selectivity index were computed in a new Methods subsection (“Tuning curves and selectivity index”) on page 50.

(6) The final panels of Figure 4 are presented as an approach to test the efficiency of biological networks. The authors seem to measure the instantaneous (and time-averaged) E-I balance while varying the adaptation parameter and then correlate this with the loss. If that is indeed the approach (it's difficult to tell), this doesn't seem to suggest a tractable experiment. Also, the conclusion is somewhat obvious: the tighter the single neuron balance, the fewer unnecessary spikes are fired. I recommend that the authors clearly explain their analysis and how they envision its application to biological data.

We indeed measured the instantaneous (and time-averaged) E-I balance while varying the adaptation parameters and then correlating this with the loss. We did not want to imply that the latter panels of Figure 4 are a means to test the efficiency or biological networks or that we are suggesting new and possibly unfeasible experiments. We see it as a way to better conceptually understand how spike triggered adaptation helps the network’s coding efficiency, by tightening the E I balance in a way that it reduces the number of unnecessary spikes. We apologize if the previous text was confusing in this respect.   We have now removed the initial paragraph of former Results Subsection (including removing the subsection title) and added new text about different effect of adaptation in E and I neurons on Page 9. We also thoroughly revised Figure 5.

(7) The external stimuli are repeatedly said to vary (or be tracked) across "multiple time scales", which might inadvertently be interpreted as (i) a single stimulus containing multiple timescales or (ii) simultaneously presented stimuli containing different timescales. These scenarios are potential targets for efficient coding through neuronal adaptation (reference 21 in the manuscript and Pozzorini et al. Nat. Neuro. 2013), but they are not addressed in the current model. I recommend the authors clarify their statements regarding timescales (and if they're up for it, acknowledge this as a limitation).

We thank the reviewer for bringing up this interesting point. To address the second point raised by the Reviewer (simultaneously presented stimuli containing multiple timescales), we performed new analyses to test the model with simultaneously presented stimuli that have different timescales. We found that the model encodes efficiently such stimuli.  We tested the case with a 3-dimensional stimulus where each dimension is an Ornstein-Uhlenbeck process with a different time constant. More precisely, we kept the time constant in the first dimension fixed (at 10 ms), and varied the time constant in the second and third dimension such that the time constant in the third dimension is doubled with respect to the second dimension. We plotted the encoding error in every stimulus dimension for E and I neurons (Fig. 8B, left plot) as well as the encoding error and the metabolic cost averaged across stimulus dimensions (Fig. 8B, right plot). The results are briefly described with text on page 13.

Regarding the case i) (single stimulus containing multiple timescales), we considered two possibilities. One possibility is that timescales of the stimulus are separable, and in this case a single stimulus containing several time scales can be decomposed in several stimuli with a single time scale each. As we assign a new set of weights for each dimension of the decomposed stimulus, this case is similar to the case ii) that we already addressed. Another possibility is that timescales of the stimulus cannot be separated. This case is not covered in the present analysis and we listed it among the limitations of the model. We revised the text (page 13) around the question of multiple time scales and included the citation of Pozzorini et al. (2013). 

(8) It is claimed that the model uses a mixed code to represent signals, citing reference 47 (Rigotti et al., Nature 2013). But whereas the model seems to use linear mixed selectivity, the Rigotti reference highlights the virtues of nonlinear mixed selectivity. In my understanding, a linearly mixed code does not enjoy the same benefits since it’s mathematically equivalent to a non-mixed code (simply rotate the readout matrix). I recommend that the authors clarify the type of selectivity used by their model and how it relates to the paper(s) they cite.

The reviewer is correct that our selectivity is a linear mixing of input variables, and differs from the selectivity in Rigotti et al. (2013) which is non-linear. We revised the sentence on page 4 to clarify better that the mixed selectivity we consider is linear and we removed Rigotti’s citation. 

(9) Reference 46 is cited as evidence that leaky integration of sensory features is a relevant computation for sensory areas. I don’t think this is quite what the reference shows. Instead, it finds certain morphological and electrophysiological differences between single pyramidal neurons in the primary visual cortex compared to the prefrontal cortex. Reference 46’ then goes on to speculate that these are differences relevant to sensory computation. This may seem like a quibble, but given the centrality of the objectivee function in normative theories, I think it's important to clarify why a particular objective is chosen.

We agree that our reference of Amatrudo et al was not the best reference and that the previous text was confusing. We thus tried to improve on its clarity. We looked at the previous theoretical efficient coding papers introducing this leaky integration and we could not find in the previous theoretical work a justification of this assumption based on experimental papers. However, there is evidence that neurons in sensory structures, and in cortical association areas respond to time varying sensory evidence by summing stimuli over time with a weight that decreases steadily going back in time from the time of firing, which suggests that neurons integrate time-varying sensory features. In many cases, these integration kernels decay approximately exponentially going back in time, and several models explaining successfully perceptual readouts of neural activity work assuming leaky integration. This suggests that the mathematical approximation of leaky integration of sensory evidence, though possibly simplistic, is reasonable.  We revised the text in this respect (page 2).  

(10) The definition of the objective function uses beta as a tuning parameter, but later parts of the text and figures refer to a parameter g_L which might only be introduced in the convex combination of Eq. 40a.

This is correct. Parameter optimization has been performed on a weighted sum of the average encoding error and cost as given by the Eq. 39a (40a in first submission), with the weighting g_L for the error versus the cost, and not the beta that is part of the objective in Eq.10. The convex combination in Eq. 39a allowed us to find a set of optimal parameters that is within biologically realistic parameter ranges, which includes realistic values for the firing threshold. The average encoding error and metabolic cost (the two terms on the right-hand side of Eq. 39a, without weighting with g_L) in our network are of the same order (see Fig 8G for the E-I model where these values are plotted separately for the optimal network). Weighing the cost with optimal beta that is in the range of ~10 would have yielded a network that optimizes almost exclusively the metabolic cost and would bias the results towards solutions with poor encoding accuracy.

To document more fully how the choice of weighting of the error with the cost (g_L) affects the optimal parameters, we now added new analysis (Fig. 8D and Supplementary Fig. S4 A-D and H) showing optimal parameters as a function of this weighting. We commented on these results in the text on pages 9-11 and 12. For further details, please see also the reply to point 1 or Reviewer 1.

(11) Figure 1J: "In E neurons, the distribution of inhibitory and of net synaptic inputs overlap". In my understanding, they are in fact identical, and this is by construction. It might help the reader to state this.

We apologize for an unclear statement. In E neurons, net synaptic current is the sum of the feedforward current and of recurrent inhibition (Eq. 29c and Eq. 42). With our choice of tuning parameters that are symmetric around zero and with stimulus features that have vanishing mean, the mean of the feedforward current is close to zero. Because of this, the mean of the net current is negative and is close to the mean of the inhibitory current. We have clarified this in the text (page 5).

(12) A few typos:

-  p1. "Minimizes the encoding accuracy" should be "maximizes..."

-  p1: "as well the progress" should be something like "as well as the progress"

-  p.11 In recorded neurons where excitatory or inhibitory. ", "where" should be "were" - Fig3: missing parentheses (B)

-  Fig4B: the 200 ticks on the y-scale are cut off.

-  Panel Fig. 5a: "stimulus" should be "stimuli".

-  Ref 24 "Efficient andadaptive sensory codes" is missing a space.

-  p. 26: "requires" should be "required".

-  On several occasions, the article "the" is missing.

We thank the reviewer for kindly pointing out the typos that we now corrected.

Reviewer #2 (Recommendations For The Authors):

I would like to give the authors more details about the two main weaknesses discussed above, so that they may address specific points in the paper. First, there is the relation to previous work. Several published articles have presented very similar results to those discussed here, including references 5, 26, 28, 32, 33, 42, 43, 48, and an additional reference not cited by the authors (Calaim et al. 2022 eLife e73276). This includes:

(1) Derivation of an E-I efficient spiking network, which is found in refs. 28, 42, 43, and 48. This is not reflected in the text: e.g., "These previous implementations, however, had neurons that did not respect Dale's law" (Introduction, pg. 1); "Unlike previous approaches (28, 48), we hypothesize that E and I neurons have distinct normative objectives...". The authors should discuss how their derivation compares to these.

We have now fully clarified on page 3 that our model builds on the seminal previous works that introduced E-I networks with efficient coding (Supplementary text in Boerlin et al. 2013, Chalk et al. 2016, Barrett et al. 2016). 

(2) Inclusion of a slow adaptation current: I believe this also appears in a previous paper (Gutierrez & Deneve 2019, ref. 33) in almost the exact same form, and is again not reflected in the text: "The strength of the current is proportional to the difference in inverse time constants ... and is thus absent in previous studies assuming that these time constants are equal (... ref. 33). Again, the authors should compare their derivation to this previous work.

We thank the reviewer for pointing this out. We sincerely apologize if our previous version did not recognize sufficiently clearly that the previous work of Gutierrez and Deneve (eLife 2019; ref 33) introduced first the slow adaptation current that is similar to spike-triggered adaptation in our model. We have made sure that the revised text recognizes it more clearly. We also explained better what we changed or added with respect to this previous work (see revised text on page 8). 

The work by Gutierrez and Deneve (2019) emphasizes the interplay between single neuron property (an adapting current in single neurons) and network property (networklevel coding through structured recurrent connections). They use a network that does not distinguish E and I neurons. Our contribution instead focuses on the adaptation in an E-I network. To improve the presentation following the Reviewer’s comment, we now better emphasize the differential effect of adaptation in E and in I neurons in revision (Fig. 5 B-D). Moreover, Gutierrez and Deneve studied the effect of adaptation on slower time scales (1 or 2 seconds) while we study the adaptation on a finer time scale of tens of milliseconds. The revised text detailed this is reported on Page 8.

(3) Background currents and physical units: Pg. 26: "these models did not contain any synaptic current unrelated to feedforward and recurrent processing" and "Moreover previous models on efficient coding did not thoroughly consider physical units of variables" - this was briefly described in ref. 28 (Boerlin et al. 2013), in which the voltage and threshold are transformed by adding a common constant, and additional aspects of physical units are discussed.

It is correct that Boerlin et al (2013) suggested adding a common constant to introduce physical units. We now revised the text to make clearer the relation between our results and the results of Boerlin et al. (2013) (page 3). In our paper, we built on Boerlin et al. (2013) and assigned physical units to computational variables that define the model's objective (the targets, the estimates, the metabolic constant, etc.). We assigned units to computational variables in such a way that physical variables (such as membrane potential, transmembrane currents, firing thresholds and resets) have the correct physical units.  We have now clarified how we derived physical units in the section of Results where we introduce the biophysical model (page 3) and specified how this derivation relates to the results in Boerlin et al. (2013).

(4) Voltage correlations, spike correlations, and instantaneous E/I balance: this was already pointed out in Boerlin et al. 2013 (ref 28; from that paper: "Despite these strong correlations of the membrane potentials, the neurons fire rarely and asynchronously") and others including ref. 32. The authors mention this briefly in the Discussion, but it should be more prominent that this work presents a more thorough study of this well-known characteristic of the network.

We agree that it would be important to comment on how our results relate to these results in Boerlin et al. (2013). It is correct that in Boerlin et al. (2013) neurons have strong correlations in the membrane potentials, but fire asynchronously, similarly to what we observe in our model. However, asynchronous dynamics in Boerlin et al. (2013) strongly depends on the assumption of instantaneous synaptic transmission and time discretization, with a “one spike per time bin” rule in numerical implementation. This rule enforces that at most one spike is fired in each time bin, thus actively preventing any synchronization across neurons. If this rule is removed, their network synchronizes, unless the metabolic constant is strong enough to control such synchronization to bring it back to asynchronous regime (see ref. 36). Our implementation does not contain any specific rule that would prevent synchronization across neurons. We now cite the paper by Boerlin and colleagues and briefly summarize this discussion when we describe the result of Fig. 3D on page 7. 

(5) Perturbations and parameters sweep: I found one previous paper on efficient spiking networks (Calaim et al. 2022) which the authors did not cite, but appears to be highly relevant to the work presented here. Though the authors perform different perturbations from this previous study, they should ideally discuss how their findings relate to this one. Furthermore, this previous study performs extensive sweeps over various network parameters, which the authors might discuss here, when relevant. For example, on pg. 8, the authors write “We predict that, if number of neurons within the population decreases, neurons have to fire more spikes to achieve an optimal population readout” – this was already shown in Calaim et al. 2022 Figure 5, and the authors should mention if their results are consistent.

We apologize for not being aware of Calaim et al. (2022) when we submitted the first version of our paper. This important study is now cited in the revised version. We have now, as suggested, performed sweeps of multiple parameters inspired by the work of Calaim. This new analysis is described extensively in reply to Weaknesses in the Public Review of reviewer 2 and is found in Fig 2, 6I and 7J and described on pages 5,11 and 13.

The Reviewer is also correct that the compensation mechanism that applies when changing the ratio of E-I neuron numbers is similar to the one described in Barrett et al. (2016) and related to our claim “if number of neurons within the population decreases, neurons have to fire more spikes to achieve an optimal population readout”. We have now added (page 11) that this prediction is consistent with the finding of Barrett et al. (2016).

With regard to the dependence of optimal coding properties on the number of neurons, we have tried to better describe similarities and differences with our work and that of Calaim et al as well as with the work of Barrett et al. (2016) which reports highly relevant results. These additional considerations are summarized in a paragraph in Discussion (page 16).

(6) Overall, the authors should distinguish which of their results are novel, which ones are consistent with previous work on efficient spiking networks, and which ones are consistent in general with network implementations of efficient and sparse coding. In many of the above cases, this manuscript goes into much more depth and study of each of the network characteristics, which is interesting and commendable, but this should be made clear. In clarifying the points listed above, I hope that the authors can better contextualize their work in relation to previous studies, and highlight what are the unique characteristics of the model presented here.

We made a number of clarifications of the text to provide better contextualization of our model within existing literature and to credit more precisely previous publications. This includes commenting on previous studies that introduced separate objective functions of E and I neurons (page 2), spike-triggered adaptation (page 8), physical units (page 3), and changes in the number of neurons in the network (page 16). 

Next, there are the claims of optimal parameters. As explained on pg. 35 (criterion for determining optimal model parameters), it appears to me that they simply vary each parameter one at a time around the optimal value. This argument appears somewhat circular, as they would need to know the optimal parameters before starting this sweep. In general, I find these optimality considerations to be the most interesting and novel part of the paper, but the simulations are relatively limited, so I would ask the authors to either back them up with more extensive parameter sweeps that consider covariations in different parameters simultaneously (as in Calaim et al. 2022). Furthermore, the authors should make sure that they are not breaking any of the required relationships between parameters necessary for the optimization of the loss function. Again, some of the results (such as coding error not being minimized with zero metabolic cost) suggests that there might be issues here. 

We thank the reviewer for this insightful suggestion. We have now added a joint sweep of all relevant model parameters using Monte-Carlo parameter search with 10.000 iterations. We randomly drew parameter configurations from predetermined parameter ranges that are detailed in the newly added Table 2. Parameters were sampled from a uniform distribution. We varied all the six model parameters studied in the paper (metabolic constant, noise intensity, time constant of single E and I neurons, ratio of E to I neurons and ratio of the mean I-I to E-I connectivity).  We now present these results on a new Figure 2. We did not find any set of parameters with lower loss than the parameters in Table 1 when the weighting of the error with the cost was in the following range: 0.4<g_L<0.81 (Fig. 2C). While our large but finite Monte-Carlo random sampling does not fully prove that the configuration we selected as optimal (on Table 1) is a global optimum, it shows that this configuration is highly efficient. Further, and as detailed in the rebuttal to the Weaknesses of the Public Review of Referee 2, analyses of the near optimal solutions are compatible with the notion (resulting from the join parameter sweep studies that we added to Figures 6 and 7) that network optimality may be influenced by joint covariations in parameters. These new results are reported in Results (page 5, 11 and 13) and in Figure 2, 6I an 7J.

Some more specific points:

(1) In general, I find it difficult to understand the scaling of the RMSE, cost, and loss values in Figures 4-7. Why are RMSE values in the range of 1-10, whereas loss and cost values are in the range of 0-1? Perhaps the authors can explicitly write the values of the RMSE and loss for the simulation in Figure 1G as a reference point.

Encoding error (RMSE), metabolic cost (MC) and average loss for a well performing network are within the range of 1-10 (see Fig. 8G or 7C in the first submission). To ease the visualization of results, we normalized the cost and the loss on Figs. 6-8 in order to plot them on the same figure (while the computation of the optima is done following the Eq. 39 and is without normalization). We have now explicitly written the values of RMSE, MC and the average loss (non-normalized) for the simulation in Fig. 1D on page 5, as suggested by the reviewer. We have also revised Fig. 4 and now show the absolute and not the relative values of the RMSE and the MC (metabolic cost). 

(2) Optimal E-I neuron ratio of 4:1 and efficacy ratio of 3:1: besides being unintuitive in relation to previous work, are these two optimal settings related to one another? If there are 4x more excitatory neurons than inhibitory neurons, won't this affect the efficacy ratio of the weights of the two populations? What happens if these two parameters are varied together?

Thanks for this insightful point. Indeed, the optima of these two parameters are interdependent and positively correlated - if we decrease the E-I neuron ratio, the optimal efficacy ratio decreases as well. To better show this relation we added figures with 2dimensional parameter search (Fig. 7J) where we varied jointly the two ratios. The red cross on the right figure marks the optimal ratios used as optimal parameters in our study. These finding are discussed on page 13.

(3) Optimal dimensionality of M=[1,4]: Again, previous work (Calaim et al. 2022) would suggest that efficient spiking networks can code for arbitrary dimensional signals, but that performance depends on the redundancy in the network - the more neurons, the better the coding. From this, I don't understand how or why the authors find a minimum in Figure 7B. Why does coding performance get worse for small M?

We optimized all model parameters with M=3 and this is the reason why M=3 is the optimal number of inputs when we vary this parameter. Our network shows a distinct minimum of the encoding error as a function of the stimulus dimensionality for both E and I neurons (Fig. 8C, top). This minimum is reflected in the minimum of the average loss (Fig. 8C, bottom). The minimum of the loss is shifted (or biased) by the metabolic cost, with strong weighting of the cost lowering the optimal number of inputs. This is discussed on pages 13-14.

Here are a list of other, more minor points, that the authors can consider addressing to make the results and text more clear:

(1) Feedforward efficient coding models: in the introduction (pg. 1) and discussion (pg. 11) it is mentioned that early efficient coding models, such as that of Olshausen & Field 96, were purely feedforward, which I believe to be untrue (e.g., see Eq. 2 of O&F 96). Later models made this even more explicit (Rozell et al. 2008). Perhaps the authors can either clarify what they meant by this, or downplay this point.

We sincerely apologize for the oversight present in the previous version of the text. We agree with the reviewer that the model in Olshausen and Field (1996) indeed defines a network with recurrent connections, and the same type of recurrent connectivity has been used by Rozell et al. (2008, 2013). The structure of the connectivity in Olshausen and Field (as well as in Rozell et al (2008)) is closely related to the structure of connectivity that we derived in our model. We have corrected the text in the introduction (page 1) to remove these errors.

(2) Pg. 2 - The authors state: "We draw tuning parameters from a normal distribution...", but in the methods, it states that these are then normalized across neurons, so perhaps the authors could add this here, or rephrase it to say that weights are drawn uniformly on the hypersphere.

We rephrased the description of how weights were determined (page 2).

(3) Pg. 2 - "We hypothesize the time-resolved metabolic cost to be proportional to the estimate of a momentary firing rate of the neural population" - from what I can see, this is not the usual population rate, which would be an average or sum of rates across the population.

Indeed, the time-dependent metabolic cost is not the population rate (in the sense of the sum of instantaneous firing rates across neurons), but is proportional to it by a factor of 1/t. More precisely, we can define the instantaneous estimate of the firing rate of a single neuron i as z_i(t) = 1/t_r r_i(t) with r_i(t) as in Eq. 7. We have clarified this in the revised text on page 3. 

(4) Pg. 3: "The synaptic strength between two neurons is proportional to their tuning similarity if the tuning similarity is positive" - based on the figure and results, this appears to be the case for I-E, E-I, and I-I connections, but not for E-E connections. This should be clarified in the text. Furthermore, one reference given in the subsequent sentence (Ko et al. 2011, ref. 51), is specifically about E-E connections, so doesn't appear to be relevant here.

We have now specified that the Eq. 24 does not describe E-E connections. We also agree that the reference (Ko et al. 2011) did not adequately support our claim and we thus removed it and revised the text on page 3 accordingly.

(5) Pg. 3: "the relative weight of the metabolic cost over the encoding error controls the operating regime of the network" and "and an operating regime controlled by the metabolic constant" - what do you mean by operating regime here?

We used the expression “operating regime” in the sense of a dynamical regime of the network.  However, we agree that this expression may be confusing and we removed it in revision. 

(6) Pg. 3: "Previous studies interpreted changes of the metabolic constant beta as changes to the firing thresholds, which has less biological plausibility" - can the authors explain why this is less plausible, or ideally provide a reference for it?

In biological networks, global variables such as brain state can strongly modulate the way neural networks respond to a feedforward stimulus. These variables influence neural activity in at least two distinct ways. One is by changing non-specific synaptic inputs to neurons, which is a network-wide effect (Destexhe and Pare, Nature Reviews Neurosci. 2003). This is captured in our model by changing the strength of the mean and fluctuations in the external currents. Beyond modulating synaptic currents, another way of modulating neural activity is by changing cell-intrinsic factors that modulate the firing threshold in biological neurons (Pozzorini et al. 2013). Previous studies on spiking networks with efficient coding interpreted the effect of the metabolic constant as changes to the firing threshold (Koren and Deneve, 2017, Gutierrez and Deneve 2019), which corresponds to cell-intrinsic factors. Here we instead propose that the metabolic constant modulates the neural activity by changing the non-specific synaptic input, homogeneously across all neurons in the network. Interpreting the metabolic constant as setting the mean of the non-specific synaptic input was necessary in our model to find an optimal set of parameters (as in Table 1) that is also biologically plausible. We revised the text accordingly (page 4).

(7) Pg. 4: Competition across neurons: since the model lacks E-E connectivity, it seems trivial to conclude that there is competition through lateral inhibition, and it can be directly determined from the connectivity. What is gained from running these perturbation experiments?

We agree that a reader with a good understanding of sparse / efficient coding theory can tell that there is competition across neurons with similar tuning already from the equation for the recurrent connectivity (Eq. 24). However, we presume that not all readers can see this from the equations and that it is worth showing this with simulations.

Following the reviewer's comment, we have now downplayed the result about the model manifesting lateral inhibition in general on page 6. We have also removed its extensive elaboration in Discussion.

One reason to run perturbation experiments was to test to what extent the optimal model qualitatively replicates empirical findings, in particular, single neuron perturbation experiments in Chettih and Harvey, 2019, without specifically tuning any of the model parameters. We found that the model reproduces qualitatively the main empirical findings, without tuning the model to replicate the data. We revised the text on page 5 accordingly.

Further reason to run these experiments was to refine predictions about the minimal amount of connectivity structure that generates perturbation response profiles that are qualitatively compatible with empirical observations. To establish this, we did perturbation experiments while removing the connectivity structure of a particular connectivity sub-matrices (E-I, I-I or I-E; Fig. S3 F). This allowed us to determine which connectivity matrix has to be structured to observe results that qualitatively match empirical findings. We found that the structure of E-I and I-E connectivity is necessary, but not the structure of I-I connectivity. Finally, we tested partial removal of the connectivity structure where we replaced the precise (and optimal) connectivity structure and imposed a simpler connectivity rule. In the optimal connectivity, the connection strength is proportional to the tuning similarity. A simpler connectivity rule, in contrast, only specifies that neurons with similar tuning share a connection, and beyond this the connection strength is random. Running perturbation experiments in such a network obeying a simpler connectivity rule still qualitatively replicated empirical results from Chettih and Harvey (2019). This is shown on the Supplementary Fig. S2F on described on page 8.

(8) Pg. 4: "the optimal E-I network provided a precise and unbiased estimator of the multidimensional and time-dependent target signal" - from previous work (e.g., Calaim et al. 2022), I would guess that the estimator is indeed biased by the metabolic cost. Why is this not the case here? Did you tune the output weights to remove this bias?

Output weights were not tuned to remove the bias. On Fig. 1H in the first submission we plotted the bias for the network that minimizes the encoding error. We forgot to specify this in the text and figure caption, for which we apologize. We now replaced this figure with a new one (Fig. 1E) where we plot the bias of the network minimizing the average loss (with parameters as in Table 1). The bias of the network minimizing the error is close to zero, B^E = 0.02 and B^I = 0.03.  The bias of the network minimizing the loss is stronger and negative, B^E = -0.15 and B^I=-0.34. In the text of Results, we now report the bias of both networks (i.e., optimizing the encoding error and optimizing the loss). We also added a plot showing trial-averaged estimates and a time-dependent bias in each stimulus dimension (Supplementary figure S1 F). Note that the network minimizing the encoding error requires a lower metabolic constant (β = 6) than the network optimizing the loss (β=14), however, the optimal metabolic cost in both networks is nonzero. We revised the text and explained these points on page 5.

(9) Pg. 4: "The distribution of firing rates was well described by a log-normal distribution" - I find this quite interesting, but it isn't clear to me how much this is due to the simulation of a finitetime noisy input. If the neurons all have equal tuning on the hypersphere, I would expect that the variability in firing is primarily due to how much the input correlates with their tuning. If this is true, I would guess that if you extend the duration of the simulation, the distribution would become tighter. Can you confirm that this is the stationary distribution of the firing rates?

We now simulated the network with longer simulation time (10 seconds of simulated time instead of 2 seconds used previously) and also iterated the simulation across 10 trials to report a result that is general across random draws of tuning parameters (previously a single set of tuning parameters was used). The reviewer is correct that the distribution of firing rates of E neurons has become tighter with longer simulation time, but distributions remain log-normal. We also recomputed the coefficient of variation (CV) using the same procedure. We updated these plots on Fig. 1F.

(10) Pg. 4: "We observed a strong average E-I balance" - based on the plots in Figure 1J, the inputs appear to be inhibition-dominated, especially for excitatory neurons. So by what criterion are you calling this strong average balance?

The reviewer is correct about the fact that the net synaptic input to single neurons in our optimal network shows excess inhibition and the network is inhibition-dominated, so we revised this sentence (page 5) accordingly.  

(11) Pg. 4: Stronger instantaneous balance in I neurons compared to E neurons - this is curious, and I have two questions: (1) can the authors provide any intuition or explanation for why this is the case in the model? and (2) does this relate to any literature on balance that might suggest inhibitory neurons are more balanced than excitatory neurons?

In our model, I neurons receive excitatory and inhibitory synaptic currents through synaptic connections that are precisely structured. E neurons receive structured inhibition and a feedforward current. The feedforward current consists of M=3 independent OU processes projected on the tuning vectors of E neurons w_i^E. We speculate that because the synaptic inhibition and feedforward current are different processes and the 3 OU inputs are independent, it is harder for E neurons to achieve the instantaneous balance that would be as precise as in I neurons. While we think that the feedforward current in our model reflects biologically plausible sensory processing, it is not a mechanistic model of feedforward processing. In biological neurons, real feedforward signals are implemented as a series of complex feedforward synaptic inputs from downstream areas, while the feedforward current in our model is a sum of stimulus features, and is thus a simplification of a biological process that generates feedforward signals. We speculate that a mechanistic implementation of the feedforward current could increase the instantaneous balance in E neurons.  Furthermore, the presence of EE connections could potentially also increase the instantaneous balance in E neurons. We revised the Discussion about these important questions that lie on the side of model limitations and could be advanced in future work. We could not find any empirical evidence directly comparing the instantaneous balance in E versus I neurons.  We have reported these considerations in the revised Discussion (page 16).

(12) Pg. 5, comparison with random connectivity: "Randomizing E-I and I-E connectivity led to several-fold increases in the encoding error as well as to significant increases in the metabolic cost" and Discussion, pg. 11: "the structured network exhibits several fold lower encoding error compared to unstructured networks": I'm wondering if these comparisons are fair. First, regarding activity changes that affect the metabolic cost - it is known that random balanced networks can have global activity control, so it is not straightforward that randomizing the connectivity will change the metabolic cost. What about shuffling the weights but keeping an average balance for each neuron's input weights? Second, regarding coding error, it is trivial that random weights will not map onto the correct readout. A fairer comparison, in my opinion, would at least be to retrain the output weights to find the best-fitting decoder for the threedimensional signal, something more akin to a reservoir network.

Thank you for raising these interesting questions. The purpose of comparing networks with and without connectivity structure was to observe causal effects of the connectivity structure on the neural activity. We agree that the effect on the encoding error is close to trivial, because shuffling of connectivity weights decouples neural dynamics from decoding weights. We have carefully considered Reviewer's suggestions to better compare the performance of structured and unstructured networks. 

In reply to the first point, we followed the reviewer's suggestion and compared the optimal network with a shuffled network that matched the optimal network in its average balance. This was achieved by increasing the metabolic constant, decreasing the noise intensity and slightly decreasing the feedforward stimulus (we did not find a way to match the net current in both cell types by changing a single parameter). As we compared the metabolic cost between the optimal and the shuffled network with matched average balance, we still found lower metabolic cost in the optimal network, even though the difference was now smaller. We replaced Fig. 3B from the first submission with these new results in Fig. 4B and commented on them in the text (page 7).

In reply to the second point, we followed reviewer’s suggestion and compared the encoding error (RMSE) of the optimal network and the network with shuffled connectivity where decoding weights are trained such as to optimally reconstruct the target signal. As suggested, we now analyzed the encoding error of the networks using decoding weights trained on the set of spike trains generated by the network using linear least square regression to minimize the decoding error. For a fair and quantitative comparison and because we did not train decoding weights of our structured model, we performed this same analysis using spike trains generated by networks with structured and shuffled recurrent connectivity. We found that the encoding error is smaller in the E population and much smaller in the I population in the structured compared to the random network. Decoding weights found numerically in the optimal network approach uniform distribution of weights that we used in our model (Fig. 4A, right). In contrast, decoding weights obtained from the random network do not converge to a uniform distribution, but instead form a much sparser distribution, in particular in I neurons (Supplementary Fig. S3 A). These additional results reported in the above mentioned figures are discussed in text on page 14.  

(13) Pg. 5: "a shift from mean-driven to fluctuation-driven spiking" and Pg. 11 "a network structured as in our efficient coding solution operates in a dynamical regime that is more stimulus-driven, compared to an unstructured network that is more fluctuation driven" - I would expect that the balanced condition dictates that spiking is always fluctuation driven. I'm wondering if the authors can clarify this.

We agree with the reviewer that networks with and without connectivity structure are fluctuation-driven, because in a mean-driven network the mean current must be suprathreshold (Ahmadian and Miller, 2021), which is not the case of either network. We removed the claim of the change from mean to fluctuation driven regime in the revised paper. We are grateful to the Reviewer for helping us tighten the elaboration of our findings.

(14) Pg. 5: "suggesting that variability of spiking is independent of the connectivity structure" - the literature of balanced networks argues against this. Is this not simply because you have a noisy input? Can you test this claim?

We thank the reviewer for the suggestion. We tested this claim by measuring the coefficient of variation in networks receiving a constant stimulus. In particular, we set the same strength in each of the M=3 stimulus dimensions and set the stimulus amplitude such as to match the firing rate of the optimal network in response to the OU stimulus. We computed the coefficient of variation in 200 simulation trials.  The removal of connectivity structure did not cause significant change of the coefficient of variation in a network driven by a constant stimulus (Fig. 4E). These additional results are discussed in text on page 7. 

We also taken the suggestion about variability of spiking being independent of the connectivity structure. We removed this claim in the revision, because we only tested a couple of specific cases where the connectivity is structured with respect to tuning similarity (fully structured, fully unstructured and partially unstructured networks). This is not exhaustive of all possible structures that recurrent connectivity may have.

(15) Pg. 6: "we also removed the connectivity structure only partially, keeping like-to-like connectivity structure and removing all structure beyond like-to-like" - can you clarify what this means, perhaps using an equation? What connectivity structure is there besides like-to-like?

In the optimal model, the strength of the synapse between a pair of neurons is proportional to the tuning similarity of the two neurons, Y_ij proportional to J_ij for Y_ij >0 (see Eq. 24 and Fig. 1C(ii)). Besides networks with optimal connectivity, we also tested networks with a simpler connectivity rule. Such a simpler rule prescribes a connection if the pair of neurons has similar tuning (Y_ij >0), and no connection otherwise. The strength of the connection following this simpler connectivity rule is otherwise random (and not proportional to pairwise tuning similarity Y_ij as it is in the optimal network). We clarified this in the revision (page 8), also by avoiding the term “like-to-like” for the second type of networks, which could indeed be prone to confusion.

(16) Pgs. 6-7: "we indeed found that optimal coding efficiency is achieved with weak adaptation in both cell types" and "adaptation in E neurons promotes efficient coding because it enforces every spike to be error- correcting" - this was not clear to me. First, it appears as though optimal efficiency is achieved without adaptation nor facilitation, i.e., when the time constants are all equal. Indeed, this is what is stated in Table 1. So is there really a weak adaptation present in the optimal case? Second, it seems that the network already enforces each spike to be errorcorrecting without adaptation, so why and how would adaptation help with this?

We agree with the Reviewer that the network without adaptation in E and I neurons is already optimal. It is also true that most spikes in an optimal network should already be error-correcting (besides some spikes that might be caused by the noise). However, regimes with weak adaptation in E neurons remain close to optimality. Spike-triggered facilitation, meanwhile, ads spikes that are unnecessary and decrease network efficiency. We revised the Fig.5 (Fig. 4 in first submission) and replaced 2-dimensional plots in Fig.4 C-F with plots that show the differential effect of adaptation in E neurons (top) and in I neurons (bottom plots) for the measures of the encoding error (RMSE), the efficiency (average loss) and the firing rate (Fig. 5B-D). On the new Fig. 5C it is evident that the loss of E and I population grows slowly with adaptation in E neurons (top) while it grows faster with adaptation in I neurons (bottom). These considerations are explained in revised text on page 9.

(17) Pg. 7: "adaptation in E neurons resulted in an increase of the encoding error in E neurons and a decrease in I neurons" - it would be nice if the authors could provide any explanation or intuition for why this is the case. Could it perhaps be because the E population has fewer spikes, making the signal easier to track for the I population?

We agree that this could indeed be the case. We commented on it in revision (page 9).

(18) Pg. 7: "The average balance was precise...with strong adaptation in E neurons, and it got weaker when increasing the adaptation in I neurons (Figure 4E)" - I found the wording of this a bit confusing. Didn't the balance get stronger with larger I time constants?

By increasing the time constant of I neurons, the average imbalance got weaker (closer to zero) in E neurons (Fig. 5G, left), but stronger (further away from zero) in I neurons (Fig. 5G, right). We have revised the text on page 9 to make this clearer.

(19) Pg. 7: Figure 4F is not directly described in the text.

We have now added text (page 9) commenting on this figure in revision.

(20) Pg. 8: "indicating that the recurrent network dynamics generates substantial variability even in the absence of variability in the external current" -- how does this observation relate to your earlier claim (which I noted above) that "variability of spiking is independent of connectivity structure"?

We agree that the claim about variability of spiking being independent of connectivity structure was overstated and we thus removed it. The observation that we wanted to report is that both structured and unstructured networks have very similar levels of variability of spiking of single neurons. The fact that much of the variability of the optimal network is generated by recurrent connections is not incompatible. We revised the related text (page 11) for clarity.

(21) Pg. 9: "We found that in the optimally efficient network, the mean E-I and I-E synaptic efficacy are exactly balanced" - isn't this by design based on the derivation of the network?

True, the I-E connectivity matrix is the transpose of the E-I connectivity matrix, and their means are the same by the analytical solution. This however remains a finding of our study. We have clarified this in the revised text (page 12).

(22) Pg. 30, eq. 25: the authors should verify if they include all possible connectivity here, or if they exclude EE connectivity beforehand.

We now specify that the equation for recurrent connectivity (Eq. 24, Eq. 25 in first submission) does not include the E-E connectivity in the revised text (page 41).

Reviewer #3 (Recommendations For The Authors):

Essential

(1)  Currently, they measure the RMSE and cost of the E and I population separately, and the 1CT model. Then, they average the losses of the E and I populations, and compare that to the 1CT model, with the conclusion that the 1CT model has a higher average loss. However, it seems to me that only the E population should be compared to the 1CT model. The I population loss determines how well the I population can represent the E population representation (which it can do extremely well). But the overall coding accuracy of the network of the input signal itself is only represented by the E population. Even if you do combine the E and I losses, they should be summed, not averaged. I believe a more fair conclusion would be that the E/I networks have generally slightly worse performance because of needing to follow Dale's law, but are still highly efficient and precise nonetheless. Of course, I might be making a critical error somewhere above, and happy to be convinced otherwise!

We carefully considered the reviewer's comment and tested different ways of combining the losses of the E and I population. We decided to follow the reviewer's suggestion and to compare the loss of the E population of the E-I model with the loss of the one cell type model. As evident already from the Fig. 8G, such comparison indeed changes the result to make the 1CT model more efficient. Also, the sum of losses of E and I neurons results in the 1CT model being more efficient than the E-I model. Note, however, the robustness of the E-I model to changes in the metabolic constant (Fig. 6C, top). The firing rates of the E-I model stay within physiological ranges for any value of the metabolic constant, while the firing rate of the 1CT model skyrocket for the metabolic constant that is lower than optimal (Fig. 8I).

We added to Results (page 14) a summary of these findings.

(2) The methods and main text should make much clearer what aspects of the derivation are novel, and which are not novel (see review weaknesses for specifics).

We specified these aspects, as discussed in more detail in the above reply to point 4 of the public review of Reviewer 1.

Request:

If possible, I would like to see the code before publication and give recommendations on that (is it easy to parse and reproduce, etc.)

We are happy to share the computer code with the reviewer and the community. We added a link to our public repository containing the computer code that we used for simulations and analysis to the preprint and submission (section “Code availability” on page 17). 

Suggestions:

(1) I believe that for an eLife audience, the main text is too math-heavy at the beginning, and it could be much simplified, or more effort could be made to guide the reader through the math.

We tried to do our best to improve the clarity of description of mathematical expressions in the main text.

(2) Generally vector notation makes network equations for spiking neurons much clearer and easier to parse, I would recommend using that throughout the paper (and not just in the supplementary methods).

We now use vector notation throughout the paper whenever we think that this improves the intelligibility of the text. 

(3) In the discussion or at the end of the results adding a clear section summarizing what the minimal requirements or essential assumptions are for biological networks to implement this theory would be helpful for experimentalists and theorists alike.

We have added such a section in Discussion (page 15). 

(5) I think the title is a bit too cumbersome and hard to parse. Might I suggest something like 'Efficient coding and energy use in biophysically realistic excitatory-inhibitory spiking networks' or 'Biophysically constrained excitatory-inhibitory spiking networks can efficiently implement efficient coding'.

We followed reviewer’s suggestion and changed the title to “Efficient coding in biophysically realistic excitatory-inhibitory spiking networks.”

(6) How the connections were shuffled exactly was not clear to me in how it was described now. Did they just take the derived connectivity, and shuffle the connections around? I recommend a more explicit methods section on it (I might have missed it).

Indeed, the connections of the optimal network were randomly shuffled, without repetition, between all neuronal pairs of a specific connectivity matrix. This allows to preserve all properties of the distribution of connectivity weights and only removes the structure of the connectivity, which is precisely what we wanted to test. We now added a section in Methods (“Removal of connectivity structure”) on pages 51-52 where we explain how the connectivity structure is removed.

(7) Figure 1 sub-panel ordering was confusing to read (first up down, then left right). Not sure if re- arranging is possible, but perhaps it could be A, B, and C at the top, with subsublabels (i) and (ii). Might become too busy though.

We followed this suggestion and rearranged the Fig. 1 as suggested by the reviewer. 

(8) Equation 3 in the main text should specify that 'y' stands for either E or I.

This has been specified in the revision (page 3). 

(9) Figure 1D shows a rough sketch of the types of connectivities that exist, but I would find it very useful to also see the actual connection strengths and the effect of enforcing Dale's law.

We revised this figure (now Fig. 1B (ii)) and added connection strengths as well as a sketch of a connection that was removed because of Dale’s law.

(10) The main text mentions how the readout weights are defined (normal distributions), but I think this should also be mentioned in the methods.

Agreed. We indeed had Methods section “Parametrization of synaptic connectivity (page 46), where we explain how readout weights are defined. We apologize if a call on this section was not salient enough in the first submission. We made sure that the revised main text contains a clear pointer to this Methods section for details. 

(11) The text seems to mix ‘decoding weights’ and ‘readout weights’.

Thanks for this suggestion to use consistent language. We opted for ‘decoding weights’ and removed ‘readout weights’.

(12) The way the paper is written makes it quite hard to parse what are new experimental predictions, and what results reproduce known features. I wonder if some sort of 'box' is possible with novel predictions that experimentalists could easily look at and design an experiment around.

We now revised the text. We clarified for every property of the model if this property is a prediction of facts that were not yet experimentally tested or if it accounts for previously observed properties of biological neurons. Please see the reply to point 4 of Reviewer 1. 

(13) Typo's etc.:

Page 5 bottom -- ("all") should have one of the quotes change direction (common latex typo, seems to be the only place with the issue).

We thank the reviewer for pointing out this typo that has been removed in revision.

He has digested only half of the spiritual message of liberalism. What half did he digest and which did he omit?

He recognized the liberal principle that a law is law regardless of moral principles. However, he neglected the second half of the principle which stipulates that just because 'law is law', does not mean it has to be obeyed.

Once again we reaffirm that Law is NOT morality, do not let it supplant morality

Reviewer #1 (Public review):

Summary:

The Authors investigated the anatomical features of the excitatory synaptic boutons in layer 1 of the human temporal neocortex. They examined the size of the synapse, the macular or the perforated appearance and the size of the synaptic active zone, the number and volume of the mitochondria, the number of the synaptic and the dense core vesicles, also differentiating between the readily releasable, the recycling and the resting pool of synaptic vesicles. The coverage of the synapse by astrocytic processes was also assessed, and all the above parameters were compared to other layers of the human temporal neocortex. The Authors conclude that the subcellular morphology of the layer 1 synapses is suitable for the functions of the neocortical layer, i.e. the synaptic integration within the cortical column. The low glial coverage of the synapses might allow the glutamate spillover from the synapses enhancing synpatic crosstalk within this cortical layer.

Strengths:

The strengths of this paper are the abundant and very precious data about the fine structure of the human neocortical layer 1. Quantitative electron microscopy data (especially that derived from the human brain) are very valuable, since this is a highly time- and energy consuming work. The techniques used to obtain the data, as well as the analyses and the statistics performed by the Authors are all solid, strengthen this manuscript, and mainly support the conclusions drawn in the discussion.

Comments on latest version:

The corrected version of the article titled „Ultrastructural sublaminar specific diversity of excitatory synaptic boutons in layer 1 of the adult human temporal lobe neocortex" has been improved thanks to the comments and suggestions of the reviewers. The Authors implemented several of my comments and suggestions. However, many of them were not completed. It is understandable that the Authors did not start a whole new series of experiment investigating inhibitory synapses (as it was a misunderstanding affecting 2 reviewers from the three). But the English text is still very hard to understand and has many mistakes, although I suggested to extensively review the use of English. Furthermore, my suggestion about avoiding many abbreviations in the abstract, analyse and discuss more the perforated synapses, the figure presentation (Figure 3) and including data about the astrocytic coverage in the Results section were not implemented. My questions about the number of docked vesicles and p10 vesicles, as well as about the different categories of the vesicle pools have not been answered neither. Many other minor comments and suggestions were answered, corrected and implemented, but I think it could have been improved more if the Authors take into account all of the reviewers' suggestions, not only some of them. I still have several main and minor concerns, with a few new ones as well I did not realized earlier, but still think it is important.

Main concerns:

(1) Epileptic patients:<br /> As all patients were epileptic, it is not correct to state in the abstract that non-epileptic tissue was investigated. Even if the seizure onset zone was not in the region investigated, seizures usually invade the temporal lobe in TLE. If you can prove that no spiking activity occured in the sample you investigated and the seizures did not invade that region, then you can write that it is presumably non-epileptic. I would suggest to write „L1 of the human temporal lobe neocortical biopsy tissue". See also Methods lines 608-612. Write only „non-epileptic" or „non-affected" if you verified it with EcoG. If this was the case, please write a few sentences about it in the Methods.

(2) About the inhibitory/excitatory synapses.<br /> Since our focus was on excitatory synaptic boutons as already stated in the title we have not analyzed inhibitory SBs.<br /> Now, I do understand that only excitatory synapses were investigated. Although it was written in the title, I did not realized, since all over the manuscript the Authors were writing synapses, and were distinguishing between inhibitory and excitatory syanpses in the text and showing numerous excitatory and inhibitory synapses on Figure 2 and discussing inhibitory interneurons in the Discussion as well. Maybe this was the reason why two reviewers out of the three (including myself) thought you investigated both types of synapses but did not differentiated between them. So, please, emphasize in the Abstract (line 40), Introduction (for ex. line 92-97) and the Discussion (line 369) that only excitatory synaptic boutons were investigated.<br /> As this paper investigated only excitatory synaptic boutons, I think it is irrelevant to write such a long section in the Discussion about inhibitory interneurons and their functions in the L1 of the human temporal lobe neocortex. Same applies to the schematic drawing of the possible wiring of L1 (Figure 7). As no inhibitory interneurons were examined, neither the connection of the different excitatory cells, only the morphology of single synaptic boutons without any reference on their origin, I think this figure does not illustrate the work done in this paper. This could be a figure of a review paper about the human L1, but is is inappropriate in this study.

(3) Perforated synapses<br /> "the findings of the Geinismann group suggesting that perforated synapses are more efficient than non-perforated ones is nowadays very controversially discussed"<br /> I did not ask the Authors to say that perforated synapses are more efficient. However, based on the literature (for ex. Harris et al, 1992; Carlin and Siekievitz, 1982; Nieto-Sampedro et al., 1982) the presence of perforated synapses is indeed a good sign of synapse division/formation - which in turn might be coupled to synaptic plasticity (Geinisman et al, 1993), increased synaptic activity (Vrensen and Cardozo, 1981), LTP (Geinisman et al, 1991, Harris et al, 2003), pathological axonal sprouting (Frotscher et al, 2006), etc. I think it is worth mentioning this at least in the Discussion.

(4) Question about the vesicle pools<br /> Results, Line 271: Still not understandable, why the RRP was defined as {less than or equal to}10 nm and {less than or equal to}20nm. Why did you use two categories? One would be sufficient (for example {less than or equal to}20nm). Or the vesicles between 10 and 20nm were considered to be part of RRP? In this case there is a typo, it should be {greater than or equal to}10 nm and {less than or equal to}20nm.<br /> The answer of the Authors was to my question raised: We decided that also those very close within 10 and 20 nm away from the PreAZ, which is less than a SV diameter may also contribute to the RRP since it was shown that SVs are quite mobile.<br /> This does not clarify why did you use two categories. Furthermore, I did not receive answer (such as Referee #2) for my question on how could you have 3x as many docked vesicles than vesicles {less than or equal to}10nm. The category {less than or equal to}10nm should also contain the docked vesicles. Or if this is not the case, please, clarify better what were your categories.

(5) Astrocytic coverage<br /> On Fig. 6 data are presented on the astrocytic coverage derived from L1 and L4. In my previous review I asked to include this in the text of the Results as well, but I still do not see it. It is also lacking from the Results how many samples from which layer were investigated in this analysis. Only percentages are given, and only for L1 (but how many patients, L1a and/or L1b and/or L4 is not provided). In contrast, Figure 6 and Supplementary Table 2 (patient table) contains the information that this analysis has been made in L4 as well. Please, include this information in the text as well (around lines 348-360).<br /> About how to determine glial elements. I cannot agree with the Authors that glial elements can be determined with high certainty based only on the anatomical features of the profiles seen in the EM. „With 25 years of experience in (serial) EM work" I would say, that glial elements can be very similar to spine necks and axonal profiles.<br /> All in all, if similar methods were used to determine the glial coverage in the different layers of the human neocortex, than it can be compared (I guess this is the case). However, I would say in the text that proper determination would need immunostaining and a new analysis. This only gives an estimatation with the possibility of a certain degree of error.

(6) Large interindividual differences in the synapse density should be discussed in the Discussion.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors investigated the anatomical features of the synaptic boutons in layer 1 of the human temporal neocortex. They examined the size of each synapse, the macular or perforated appearance, the size of the synaptic active zone, the number and volume of the mitochondria, and the number of synaptic and dense core vesicles, also differentiating between the readily releasable, the recycling, and the resting pool of synaptic vesicles. The coverage of the synapse by astrocytic processes was also assessed, and all the above parameters were compared to other layers of the human temporal neocortex. The authors conclude that the subcellular morphology of the layer 1 synapses are suitable for the functions of the neocortical layer, i.e. the synaptic integration within the cortical column. The low glial coverage of the synapses might allow increased glutamate spillover from the synapses, enhancing synaptic crosstalk within this cortical layer.

Strengths:

The strengths of this paper are the abundant and very precious data about the fine structure of the human neocortical layer 1. Quantitative electron microscopy data (especially that derived from the human brain) are very valuable since this is a highly time- and energy-consuming work. The techniques used to obtain the data, as well as the analyses and the statistics performed by the authors are all solid, strengthen this manuscript, and mainly support the conclusions drawn in the discussion.

We would like to thank reviewer#1 for his very positive comments on our manuscript stating that such data about the fine structure of the human neocortex are are highly relevant.

Weaknesses:

There are several weaknesses in this work. First, the authors should check and review extensively for improvements to the use of English. Second, several additional analyses performed on the existing data could substantially elevate the value of the data presented. Much more information could be gained from the existing data about the functions of the investigated layer, of the cortical column, and about the information processing of the human neocortex. Third, several methodological concerns weaken the conclusions drawn from the results.

We would like to thank the reviewer for his critical and thus helpful comments on our manuscript. We took the first comment of the reviewer concerning the English and have thus improved our manuscript by rephrasing and shortening sentences. Secondly, according to the reviewer several additional analyses should be performed on the existing data, which could substantially elevate the value of the data presented. We will implement some of the suggestions in the improved version of the manuscript where appropriate. We will address a more detailed answer to the reviewer’s queries in her/his suggestions to the authors (see below). However, the reviewer states himself: “The techniques used to obtain the data, as well as the analyses and the statistics performed by the authors are all solid, strengthen this manuscript, and mainly support the conclusions drawn in the discussion”.

Reviewer #2 (Public review):

Summary:

The study of Rollenhagen et al. examines the ultrastructural features of Layer 1 of the human temporal cortex. The tissue was derived from drug-resistant epileptic patients undergoing surgery, and was selected as far as possible from the epilepsy focus, and as such considered to be non-epileptic. The analyses included 4 patients with different ages, sex, medication, and onset of epilepsy. The manuscript is a follow-on study with 3 previous publications from the same authors on different layers of the temporal cortex:

Layer 4 - Yakoubi et al 2019 eLife

Layer 5 - Yakoubi et al 2019 Cerebral Cortex

Layer 6 - Schmuhl-Giesen et al 2022 Cerebral Cortex.

They find, that the L1 synaptic boutons mainly have a single active zone, a very large pool of synaptic vesicles, and are mostly devoid of astrocytic coverage.

Strengths:

The manuscript is well-written and easy to read. The Results section gives a detailed set of figures showing many morphological parameters of synaptic boutons and glial elements. The authors provide comparative data of all the layers examined by them so far in the Discussion. Given that anatomical data in the human brain are still very limited, the current manuscript has substantial relevance. The work appears to be generally well done, the EM and EM tomography images are of very good quality. The analysis is clear and precise.

We would like to thank the reviewer for his very positive evaluation of our paper and the comments that such data have a substantial relevance, in particular in the human neocortex. In contrast to reviewer#1, this reviewer’s opinion is that the manuscript is well written and easy to read.

Weaknesses:

One of the main findings of this paper is that "low degree of astrocytic coverage of L1 SBs suggests that glutamate spillover and as a consequence synaptic cross-talk may occur at the majority of synaptic complexes in L1". However, the authors only quantified the volume ratio of astrocytes in all 6 layers, which is not necessarily the same as the glial coverage of synapses. In order to strengthen this statement, the authors could provide 3D data (that they have from the aligned serial sections) detailing the percentage of synapses that have glial processes in close proximity to the synaptic cleft, that would prevent spillover.

We agree with the reviewer that we only quantified the volume ratio of the astrocytic coverage but not necessarily the percentage of synapses that may or not contribute to the formation of the ‘tripartite’ synapse. As suggested, we will re-analyze our material with respect to the percentage of coverage for individual synaptic boutons in each layer and will implement the results in the improved version of the manuscript. However, since this is a completely new analysis that is time-consuming we would like to ask the reviewer for additional time to perform this task.

A specific statement is missing on whether only glutamatergic boutons were analyzed in this MS, or GABAergic boutons were also included. There is a statement, that they can be distinguished from glutamatergic ones, but it would be useful to state it clearly in the Abstract, Results, and Methods section what sort of boutons were analyzed. Also, what is the percentage of those boutons from the total bouton population in L1?

We would like to thank the reviewer for this comment. Although our title clearly states, we focused on quantitative 3D-models of excitatory synaptic boutons, we will point out that more clearly in the Methods and Result chapters. Our data support recent findings by others (see for example Cano-Astorga et al. 2023, 2024; Shapson-Coe et al. 2024) that have evaluated the ratio between excitatory vs. inhibitory synaptic boutons in the temporal lobe neocortex, the same area as in our study, which was between 10-15% inhibitory terminals but with a significant layer and region specific difference. We will include the excitatory vs. inhibitory ratio and the corresponding citations in the Results section.

Synaptic vesicle diameter (that has been established to be ~40nm independent of species) can properly be measured with EM tomography only, as it provides the possibility to find the largest diameter of every given vesicle. Measuring it in 50 nm thick sections results in underestimation (just like here the values are ~25 nm) as the measured diameter will be smaller than the true diameter if the vesicle is not cut in the middle, (which is the least probable scenario). The authors have the EM tomography data set for measuring the vesicle diameter properly.

We partially disagree with the reviewer on this point. Using high-resolution transmission electron microscopy, we measured the distance from the outer-to-outer membrane only on those synaptic vesicles that were round in shape with a clear ring-like structure to avoid double counts and discarded all those that were only partially cut according to criteria developed by Abercrombie (1946) and Boissonnat (1988). We assumed that within a 55±5 nm thick ultrathin section (silver to gray interference contrast) all clear-ring-like vesicles were distributed in this section assuming a vesicle diameter between 25 to 40nm. For large DCVs, double-counts were excluded by careful examination of adjacent images and were only counted in the image where they appeared largest.

In addition, we have measured synaptic vesicles using TEM tomography and came to similar results. We will address this in Material and Methods that both methods were used.

It is a bit misleading to call vesicle populations at certain arbitrary distances from the presynaptic active zone as readily releasable pool, recycling pool, and resting pool, as these are functional categories, and cannot directly be translated to vesicles at certain distances. Indeed, it is debated whether the morphologically docked vesicles are the ones, that are readily releasable, as further molecular steps, such as proper priming are also a prerequisite for release.

We thank the reviewer for this comment. However, nobody before us tried to define a morphological correlate for the three functionally defined pools of synaptic vesicles since synaptic vesicles normally are distributed over the entire nerve terminal. As already mentioned above, after long and thorough discussions with Profs. Bill Betz, Chuck Stevens, Thomas Schikorski and other experts in this field we tried to define the readily releasable (RRP), recycling (RP) and resting pools by measuring the distance of each synaptic vesicle to the presynaptic density (PreAZ). Using distance as a criterion, we defined the RRP including all vesicles that were located within a distance (perimeter) of 10 to 20 nm from the PreAZ that is less than an average vesicle diameter (between 25 to 40 nm). The RP was defined as vesicles within a distance of 60-200 nm away, still quite close but also rapidly available on demand and the remaining ones beyond 200 nm were suggested to belong to the resting pool. This concept was developed for our first publication (Sätzler et al. 2002) and this approximation since then is very much acknowledged by scientist working in the field of synaptic neuroscience and computational neuroscientist. We were asked by several labs worldwide whether they can use our data of the perimeter analysis for modeling. We agree that our definition of the three pools can be seen as arbitrary but we never claimed that our approach is the truth but nothing as the truth. Concerning the debate whether only docked vesicles or also those very close the PreAZ should constitute the RRP we have a paper in preparation using our perimeter analysis, EM tomography and simulations trying to clarify this debate. Our preliminary results suggest that the size of the RRP should be reconsidered.

Tissue shrinkage due to aldehyde fixation is a well-documented phenomenon that needs compensation when dealing with density values. The authors cite Korogod et al 2015 - which actually draws attention to the problem comparing aldehyde fixed and non-fixed tissue, still the data is non-compensated in the manuscript. Since all the previous publications from this lab are based on aldehyde fixed non-compensated data, and for this sake, this dataset should be kept as it is for comparative purposes, it would be important to provide a scaling factor applicable to be able to compare these data to other publications.

We thank the reviewer for his suggestion. However, for several reasons we did not correct for shrinkage caused by aldehyde fixation. There are papers by Eyre et al. (2007) and the mentioned paper by Korogod et al. 2015 that have demonstrated that cryo-fixation reveals larger numbers of docked synaptic vesicles, a smaller glial volume, and a less intimate glial coverage of synapses and blood vessels compared to chemical fixation. Other structural subelements such as active zone size and shape and the total number of synaptic vesicles remained unaffected. In two further publications Zhao et al. (2012a, b) investigating hippocampal mossy fiber boutons using cryo-fixation and substitutions came to similar results with respect to bouton and active zone size and number and diameter of synaptic vesicles compared to aldehyde-fixation as described by Rollenhagen et al. 2007 for the same nerve terminal. This was one of the reasons not correcting for shrinkage. In addition, all cited papers state that chemical fixation in general provides a much better ultrastructural preservation of tissue samples when compared with cryo-fixation and substitution where optimal preservation is only regional within a block of tissue and therefore less suitable for large-scale ultrastructural analyses as we performed.

Reviewer #3 (Public review):

Summary:

Rollenhagen et al. offer a detailed description of layer 1 of the human neocortex. They use electron microscopy to assess the morphological parameters of presynaptic terminals, active zones, vesicle density/distribution, mitochondrial morphology, and astrocytic coverage. The data is collected from tissue from four patients undergoing epilepsy surgery. As the epileptic focus was localized in all patients to the hippocampus, the tissue examined in this manuscript is considered non-epileptic (access) tissue.

Strengths:

The quality of the electron microscopic images is very high, and the data is analyzed carefully. Data from human tissue is always precious and the authors here provide a detailed analysis using adequate approaches, and the data is clearly presented.

We are very thankful to the reviewer upon his very positive comments about our data analysis and presentation.

Weaknesses:

The study provides only morphological details, these can be useful in the future when combined with functional assessments or computational approaches. The authors emphasize the importance of their findings on astrocytic coverage and suggest important implications for glutamate spillover. However, the percentage of synapses that form tripartite synapses has not been quantified, the authors' functional claims are based solely on volumetric fraction measurements.

We thank the reviewer for his critical comments on our findings concerning the layer-specific astrocytic coverage as also suggested by reviewer#2. As already stated above we will analyze the astrocytic coverage and the layer-specific percentage of astrocytic contribution to the ‘tripartite’ synapse in more detail. We are, however, a bit puzzled about the comment that structural anatomists usually receive that our study only provides morphological details. Our thorough analysis of structural and synaptic parameters of synaptic boutons underlie and might even predict the function of synaptic boutons in a given microcircuit or network and will thus very much improve our understanding and knowledge about the functional properties of these structures, in particular in the human brain where such studies are still quite rare. The main goal of our studies in the human neocortex was the quantitative morphology of synaptic boutons and thus the synaptic organization of the cortical column, layer by layer which to our knowledge is the first such detailed study undertaken in the human brain. Our efforts have set a golden standard in the analysis of synaptic boutons embedded in different microcircuits und is meanwhile internationally very well accepted.

The distinction between excitatory and inhibitory synapses is not clear, they should be analyzed separately.

As already stated above in response to reviewer#1 our study focused on excitatory synaptic boutons since they represent the majority of synapses. However, in the improved version of our manuscript in the Material and Method section we included a paragraph with structural criteria to distinguish excitatory from inhibitory terminals (see also our comment to reviewer#1 concerning this point) including appropriate citations.

The text connects functional and morphological characteristics in a very direct way. For example, connecting plasticity to any measurement the authors present would be rather difficult without any additional functional experiments. References to various vesicle pools based on the location of the vesicles are also more complex than suggested in the manuscript. The text should better reflect the limitations of the conclusions that can be drawn from the authors' data.

We thank the reviewer for this comment. However, it has been shown by meanwhile numerous publications that the shape and size of the active zone together with the pool of synaptic vesicles and the astrocytic coverage critically determines synaptic transmission and synaptic strength, but can also contribute to the modulation of synaptic plasticity (see also citations within the text). It has been shown that synaptic boutons can switch upon certain stimulation conditions to different modes of release (uni- vs. multiquantal, uni- vs multivesicular release) and from asynchronous to synchronous release leading also to the modulation of synaptic short- and long-term plasticity. To the second comment: When we started with our first paper about the Calyx of Held – principal neuron synapse in the MNTB (Sätzler et al. 2002) we tried to define a morphological correlate for the three functionally defined pools. As already mentioned above in our reply to the other two reviewers, this is rather difficult since synaptic vesicles are normally distributed over the entire nerve terminal. After long and thorough discussions with Bill Betz, Chuck Stevens and other leading scientist in the field of synaptic neuroscience, we together with Bert Sakmann tried to define a morphological correlate for the functionally defined pools using a perimeter analysis. We defined the readily releasable pool as vesicles 10 to 20 nm away from the presynaptic active zone, the recycling pool as those in 60-200 nm distance and the remaining as those belonging to the resting pool. However, it has been shown by capacitance measurements (see for example Hallermann et al 2003), FM1-43 investigations (see for example Henkel et al. 1996) and high-resolution electron microscopy (see for example Schikorski and Stevens 2001; Schikorski 2014) that our estimate of the RRP nearly perfectly matches with the functionally defined pools at hippocampal and cortical synapses (Silver et al. 2003). In addition, in one of our own papers (Rollenhagen et al. 2018) we also estimated the RP functionally from trains of EPSPs using an exponential fit analysis and came to similar results upon its size using the perimeter analysis.

Of course, as stated by the reviewer the scenario could be more complex, using other criteria but we never claimed that our morphologically defined pools are the truth but nothing as the truth but we believe it offers a quite good approximation.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Abstract:

Avoid the numerous abbreviations in the abstract. The paragraph describing the results obtained in this study is too short. Include more results, such as the size of the active zone, the proportion of perforated synapses, the ratio of synapses terminating on dendrites/spines, the percentage of volume occupied by mitochondria, etc. In the last paragraph, compare the layer-specific data to other layers of the neocortex before writing the concluding sentence.

To meet the word limits of the abstract (150 words) defined by eLife we had to use abbreviations. We followed the suggestions by the reviewer and expanded our abstract by adding the proportion of macular vs. perforated active zone and the percentage of mitochondria within an SB. However, we did not include the comparison of structural parameters in the Abstract since this is discussed thoroughly in the MS at other places (see Results and Discussion).

Results:

First of all, wonderful data! Lots of work, very valuable quantitative electron microscopy results.

Main concerns:

Adding several analyses would give much more information about the cortical synaptic organization. It would be very useful to differentiate between excitatory and inhibitory terminals (and give their ratio) and include this information in all different analyses, such as in the SV number, SV pool analysis, mitochondrion analysis, etc., that would give functional information as well. You have all the data for this, and you know how to differentiate between inhibitory and excitatory synapses, it can be done. We could see the possible morphological differences between excitatory and inhibitory synapses (maybe one is larger/has more SVs, etc. than the other). Based on these possible differences conclusions could be drawn about functional hypotheses, such as one or the other is more efficient in inducing postsynaptic potentials, excitation or inhibition is more pronounced in layer 1, etc. Furthermore, looking at the ratio of perforated synapses, we could gain information about the formation of new synapses. Maybe there is a difference between excitatory and inhibitory circuits in this point of view.

To the first point: Since our focus was on excitatory synaptic boutons as already stated in the title we have not analyzed inhibitory SBs. To do so, we have to re-analyze our complete data which is time-consuming and an additional workload. However, we can give a ratio excitatory vs. inhibitory synaptic boutons which was between 10-15% but with layer-specific differences. Our finding are in good agreement with a recent publication in Science by the Lichtman group (Shapson-Coe et al. 2024) and work by the DeFelipe group (Cano-Astorga et al. 2023, 2024) estimating the number of inhibitory boutons in different layers of the temporal lobe neocortex as we did by 10-15%. We included a small paragraph about inhibitory synapses, their percentage and included the citations in our Results section. Concerning the ratio between macular, non-perforated vs. perforated active zones we stated the majority of synaptic boutons were of the macular, non-perforated type (~75%; see improved version of the MS). If perforated, this was found predominantly on the postsynaptic site, but quite rare in L1 SBs. Since GABAergic terminals had only a small or no clearly visible PSD this would be hard to look at.

To the last point, it has been demonstrated that the number of dense core vesicles and their fusion with the presynaptic density could be a critical factor in the build-up of the active zone. In addition, the findings of the Geinismann group suggesting that perforated synapses are more efficient than non-perforated ones is nowadays very controversially discussed since other factors such as size of the active zone (see for example Matz et al. 2010; Holderith et al. 2012) and the astrocytic coverage contribute to synaptic efficacy and strength.

Related to this topic: although in the case of rat CA1 pyramidal cells all inhibitory synapses terminated on dendritic shafts (Megias et al., Neuroscience 2001), please be aware that both excitatory and inhibitory synapses can terminate on both dendritic shafts and spines in humans (inhibitory synapses are though rare on spines, usually less than 10%, but they do exist, see for example Wittner et al, Neuroscience, 2001). Please, define the excitatory/inhibitory nature of the synapses based on morphological features (not on their postsynaptic target), i.e., flattened vesicles and thin postsynaptic density for GABAergic synapses, whereas larger, round vesicles and thick postsynaptic density for glutamatergic synapses. Anyway, the ratio of excitatory and inhibitory synapses on dendrites and spines in the two sublamina would also give useful information about the synaptic organization of the human neocortical layer 1.

We are aware that not all terminals targeting on spines are excitatory, in turn it has been shown that not all terminals on shafts were inhibitory as long thought (Silver et al. 2003). However, as stated by the reviewer their abundancy on spines is rather low. At the moment it is rather unclear which functional impact inhibitory terminals on spines have, despite a local inhibition (see for example Kubota et al. eLife 2015), and thus their role is rather speculative since excitatory synapses are the predominant class on dendritic spines. As already stated above the ratio of excitatory vs. inhibitory terminals is between 10-15% and not significantly different between the two sublaminae. We are willing to add this in the results section (see in the improved version of the manuscript).

(2) About the glial coverage: Please, specify how glial elements were determined. What were the morphological features specific to astroglial processes? In Figure 5, how could we know whether the glial element marked by green is not a spine neck? The lack of morphological features specific to glial processes makes this analysis weak. The most accurate would be to make it with the aid of GFAP staining. I know this is not possible with your existing data, but at least, provide information on how glial processes were identified.

We used the criteria first described by Peters et al. (1991) and Ventura and Harris (1999) identifying astrocytic profiles by their irregular stellate shape, relatively clear cytoplasm, numerous glycogen granules and bundles of intermediate filaments. After more than 20 years of structural investigations, we hope that the reviewers will believe us that we can identify astrocytic processes at the high-resolution TEM level. In some of our publications (Rollenhagen et al. 2007; 2015; 2018; Yakoubi et al. 2019a) we have used glutamine synthetase pre-embedding immunhistochemistry to identify astrocytic processes, but a disadvantage of this method is the reduction of the ultrastructural preservation of the tissue. We have included the criteria to identify astrocytic processes of glial coverage in our manuscript together with the two citations (see improved version of the manuscript).

(3) The authors state that the total number of SVs was very variable. How was the distribution of the number of SVs? Homogenous distribution suggests that different types of synapses cannot be distinguished based on their morphological features, whereas distribution with more than one peak would suggest that different types of synapses are present in L1, and that they can be differentiated by their appearance (number of SVs, for example). This might be also related to the type of synapse (i.e., excitatory or inhibitory). The same applies to the number of RP and resting pool SVs.

To look for differences in structural and synaptic parameters that can further classify synaptic boutons we have performed a hierarchical cluster and multivariance analysis. However, it turned out that according to structural and functional parameters no further classification into subtypes could be done.

(4) The authors should check and review extensively for improvements to the use of English. The Results and Discussion sections contain many sentences which are not easy to understand. They have either a too complicated structure, or they are incomplete and hard to follow. Few examples: "The RRP/PreAZ at p20 nm criterium was on average 19.05 {plus minus} 17.23 SVs (L1a: 25.04 {plus minus} 21.09 SVs and L1b: 13.07 {plus minus} 13.87SVs) and thus nearly 2-fold larger for L1a." If you take out the parenthesis, the sentence has no meaning. "The majority of SBs in L1 of the human TLN had a single at most three AZs that could be of the non-perforated macular or perforated type comparable with results for other layers in the human TLN but by ~1.5-fold larger than in rodent and non-human primates." Rephrase these types of sentences, please.

We partially agree with the reviewer. We have improved our manuscript by rephrasing and shortening sentences.

Other suggestions:

(1) Put the synaptic density part after the description of the neuronal and synaptic composition part, it is more logical this way (i.e., first qualitative description, the distinction between sublayers, then quantitative data). Please write down in the description of the neuronal and synaptic composition part how L1a and L1b were differentiated (see also my comment on Figure 1).

We agree with the reviewer and did the change according to the suggestion. For a better understanding, we have also expanded the neuronal and synaptic description of the two sublaminae in L1.

(2) Introduce a list of abbreviations at the beginning, that would help.

It is quite unusual to provide a list of abbreviations in eLife. However, when used first the full meaning of the abbreviations is now given.

(3) What is cleft width? Usually, it refers to the distance between the pre- and the postsynaptic membrane, but here, I think it refers to the size (diameter) of the active zone. Please, clarify in the Result section (as it appears earlier than the Methods section, where it is explained). I would probably use the expression "synaptic cleft size" instead of "synaptic cleft width" to avoid misunderstanding.

We thank the reviewer for the suggestion and used synaptic cleft size for better clarity and have transferred the sentence from the Material and Methods to the Results section.

(4) The description of the different SVs (RRP, RP, etc.) is not clear in lines 236-242. What does it mean, that RRP vesicles are located {less than or equal to}10 nm and {less than or equal to}20 nm from the active zone? Explain, why the two different distance criteria were used. Furthermore, how were the vesicles located at p20-p60 defined? Why were these vesicles not considered in the determination of the different pools?

As stated in the public review to the reviewers concern we have tried to define a morphological correlate to the three functionally defined pools. After thorough discussions, with leading scientists in the field of synaptic neuroscience we have decided to use the distance of individual vesicles from the PreAZ and sort vesicles upon these criteria. One can argue that this approach is random, however, these distance criteria were described by Rizzoli and Betz (2004, 2005) and Denker and Rizzoli (2010). As also stated in the public review there is still a controversial discussion whether only docked or omega-shaped SVs constitute the RRP. We decided that also those very close within 10 and 20 nm away from the PreAZ, which is less than a SV diameter may also contribute to the RRP since it was shown that SVs are quite mobile.

(5) Please, explain how the number of docked vesicles can be 3x larger in L1b, than the number of vesicles located at p10? Docked vesicles are the closest (with the membrane touching the PreAZ)... if this comes from the fact that another pool of boutons was used for the EM tomography analysis, then the entire pool of boutons analyzed, then it means that the selection of boutons for the EM tomography is highly biased. This also implies that EM tomography data are most probably not valid for the entire L1b. The difference might also come from the different ratios of dendrite/spine synapses included in the two different analyses. In this case, it would be helpful to distinguish between synapses terminating on dendrites/spines and analyse them separately (same as for inhibitory/excitatory, which is not exactly the same as dendrite/spine!). Different n numbers of synapses are given in the text (n=25, 25, 25 25) and in Table 2 (n=91, 98, 87, and 84) for the analysis of the docked vesicles, please, correct this.

This is a correct value and thus there is a nearly 3-fold difference. The TEM tomography was carried out on the same blocks that have been used for our 3D-volume reconstructions. To carry out TEM tomography we had to use thicker sections (250 nm) to look for complete SBs as we also did in our serial sections, but of course, we could not quantify the same SBs. The completeness of SBs was one of our main criteria to reconstruct structural and synaptic parameters. The second was that the synaptic cleft was cut perpendicular. Only SBs that met these criteria were chosen for further quantitative analysis. In this respect we are of course biased in both methods.

Secondly, as already stated we did not quantify inhibitory terminals in serial sections. However, we did not find significant differences between shaft vs. spine synapses.

Finally, in Table 2 the total number of ‘docked’ SVs is given analyzed from the total number of SBs analyzed.

Discussion:

Please include the recent findings of human L1 neurons, including the "rosehip" cells in the L1 neuronal network, see Boldog et al., Nat Neurosci 2018. It would be also useful to consider in the discussion the human-specific cortical synchrony and integration phenomena derived from in vitro data (Mansvelder, Lein, Tamas, Wittner, Larkum, Huberfeld labs, etc.), and how the synaptic morphology can be related to these.

We thank the reviewer and include the reference in our chapter functional significance.

Figures and Tables:

Figure 1: In the legend, it is written that CR cells are marked by an asterisk, but on the figure it is marked by arrowheads. H: I would put the dashed line slightly lower, just above the two neuronal cell bodies. Now it looks like in the middle of the astrocytic layer. One of the asterisks marking the CR cell is not above the nucleus of that cell. I: the gabaergic neuron is outside of the framed area. I would delete the frame, anyway, the arrowheads and the asterisk are enough to show what the authors want to show.

We have changed the Figure according to the suggestions raised by the reviewer.

Figure 3: The transparent yellow is not visible. It is a bit disturbing that the contours of the boutons are not visible, I would make the transparent yellow stronger (less transparent). The SVs in green/magenta will be still visible.

We wanted to highlight the internal subelements of SBs and thus made the covering transparent but we think it is still visible.

Figure 6C: The data concerning other layers than L1 are most probably taken from other publications of the research group. One is cited (for L6), but not the others. Please correct this, or if not, then write this in the Results and Methods.

We changed the citation in the improved version of the manuscript. We overlooked that the values for L4 and L5 were already published in Schmuhl-Giesen et al. 2022.

Table 1: What does central and lateral cleft width mean in Table 1? Furthermore, please, give the name for abbreviations CV and IQR in Tables 1 and 2.

The measurements of the synaptic cleft are now described in detail in the Results section. We now have given the full names for CV and IQR in the legends of tables 1 and 2.

Supplemental Figures 1 and 2: Why Hu01 and Hu02 are twice? What is the difference? Based on the figure legend, it is L1a and L1b? If yes, please, indicate on the figure or in the legend.<br /> Supplemental Table 1: What is TLE in the case of Hu_04? If it is temporal lobe epilepsy, then why age at epilepsy onset is missing?

Yes, Hu01 and Hu02 were selected for both L1a and L1b in separate serial sections preparations each. We indicated this now in the figure legend. Concerning Hu_04, unfortunately we do not have any further information about the medical background of the patient.

Supplemental Table 1 (Patient table), that there are many abbreviations explained which do not appear in the table (lBAZ: Brivaracetam CBZ: Carbamazepine; CLB: Clobazam; ESL: Eslicarbazepin; GGL: Ganglioglioma, etc.), please check and correct.

We have removed the unnecessary abbreviations.

Other minor suggestions:

What is Pr? Please, give the name a first appearance (line 368).

We explained Pr (release probability) when used for the first time.

Give the name for t-LDT, please (lines 442-443).

We explained t-LTD (timing-dependent long-term depression) when used for the first time.

Typo in line 169: DCW instead of DCV (dense core vesicle), DCV is used in the figure legends.

We changed DCW to DCV.

Typo in line 190: Yokoubi instead of Yakoubi (reference).

We changed Yokoubi to Yakoubi.

Typo in line 237: Rizzoloi instead of Rizzoli (reference).

We changed Rizzoloi to Rizzoli.

Line 229-230: One reference is not inserted properly - Piccolo and Bassoon.

The reference of Schoch and Gundelfinger and Murkherjee to the build-up of the active zone and the role of DCV containing Piccolo and Bassoon are properly cited in the text.

Typo in line 398: exit instead of exist.

Corrected

Typo in line 700: Reynolds (1063) instead of 1963.

Corrected

Reviewer #2 (Recommendations for the authors):

Abstract:

The last sentence seems far-fetched, and unrelated to the manuscript. How mostly single active zone boutons can "mediate, integrate and synchronize contextual and cross-modal information, enabling flexible and state-dependent processing of feedforward sensory inputs from other layers of the cortical column"? Which of the anatomical findings of the manuscript led to these conclusions?

According to the review by Schuman et al. (2021) layer 1 is regarded as a layer that mediate, integrate and synchronize contextual and cross-modal information, enabling flexible and state-dependent processing of feedforward sensory inputs from other layers of the cortical column to which the structural quantitative 3D- models of SBs contribute since they are an integral element connecting neurons and building networks.

I am also puzzled by the authors' statement in more than one place of the manuscript that "L1a can be characterized as a predominantly astrocytic sublamina". If the L1 contains the lowest measured volume ratio of glial processes (Figure 6), then this description does not seem to hold. Please rephrase.

The reviewer is right and we rephrased the sentences for more clarity in the improved version of our manuscript.

Results:

The authors find large inter-patient variability in the synapse density at L1, which raises the issue of what were the criteria to include certain patients in the analyses. Apparently, these are different from the ones analysed in their previous papers, and all the provided parameters were different (sex, age, medication, onset of epilepsy), and any of them can result in altered synapse density.

First, we have not used all patients for this study. Secondly, it was not possible to use all patients for all six layers.

It would be useful to add a panel for Figure 1 with synapse density across the different layers, as they provide this data in the Discussion.

We implemented a Supplementary Table 1 with the synaptic density values over all layers compared in the Discussion.

I cannot find Source Data 1 in the manuscript although it is referred to in more than 1 place (e.g. page 5 line 100).

Source data were uploaded when our manuscript was submitted directly to eLife as Supplemental Material. However, as stated by bioRxiv ‘any Supplemental Materials associated with this manuscript have not been transferred to bioRxiv to avoid the posting of potentially sensitive information’ all source data have not been uploaded to the preprint server.

Page 5 line 100 the correct value is 7.3*107 or rather 108?

We corrected the value in the improved version of the MS.

It would be nice to put the synapse density values into context by comparing them to e.g. mouse, rat, or monkey data.

Since we are working on the human temporal lobe neocortex we avoided to compare those data with those estimated in experimental animals. In addition as discussed by DeFelipe et al. (1999) different methods were used to quantify synaptic density in experimental animals so these results are difficult to compare.

Page 5 Line 117 CR-cells stands for Cayal-Retzius cells?

CR-cells is the abbreviation for Cajal-Retzius cells.

Page 6 Line 146 repeated sentence.

We deleted the repeated sentence.

Page 7 Line 154 "file-scale TEM" ??

We replaced file-scale by fine-scale.

Page 7 Line 164 "GABAergic synapses identified by the smaller more spherical SVs". With this fixation condition, GABAergic vesicles are more ovoid than glutamatergic ones. What were the criteria to distinguish them?

To our knowledge in meanwhile numerous publications using the same fixation inhibitory terminals contain more spherical and smaller and not roundish synaptic vesicles and showed no clear prominent PSDs as described in our paper. We have addressed that more clearly in the results section of the improved version of the MS.

Page 8 line 197 "The majority (~98%) of SBs in L1a and L1b had only a single (Figures 2C-E, 3A-C, E) at most two or three AZs" is in striking contrast with the other statement from page 7 Line 163 "Numerous SBs in both sublaminae were seen to establish either two or three synaptic contacts on the same spine or dendrite". Which of these statements is valid? Please provide exact quantification for this statement and decide which one is true.

It is true that the majority of synaptic boutons had a single active zone. However, for example on a spine not only a single but also two or three SBs can be found. We have rephrased this sentence for more clarity.

Page 9 Line 206 "L1 AZs did not show a large variability in size as indicated by the low SD, CV, and variance (Table 1)" Is this inter-patient variance of mean values? As in Supplementary Figure 1, both the SBs volume and PreAZ area show large variability in a given patient sample. Only the inter-patient variability of mean values seems low. Please state it clearly throughout the MS for other datasets as well.

For clarity concerning the variability between patients and structural parameters we have generated box plots (Suppl. Figures 1 and 2).

Page 9 Line 208 data is on Figure 5A and not 8A.

We thank the reviewer and corrected the citation of the Figure

Page 12 Line 295 how can the number of docked vesicles for L1b be larger than the one measured by the perimeter p10 nm? This later should contain the docked and PreAZ membrane proximal pool as well. This difference is even larger if we assume, that at EM tomography only partial AZs were analysed in a 200 nm thick section, not the entire AZ as for the perimeter measurement. Can the authors provide density estimates by dividing the docked / p10 nm vesicle numbers with the AZ area and comparing them?

This is a result comparing both methods. To the second concern: As stated in the text only synaptic boutons were the active zone can be followed from the beginning to its end and were the synaptic cleft was cut perpendicular were included in the TEM tomography sample as we also did in our 3D-volume reconstructions.

Methods:

Page 25 Line 624 While the PSD area can be equivocally measured, due to the dense appearance of the PSD on the EM images, the PreAZ is more difficult to outline due to lack of evident anatomical markers except the synaptic cleft (the dense material is much thinner). That is why in many publications the PreAZ area is considered to be identical to the PSD area. What are the anatomical criteria used here for the PreAZ? Why do the authors correct the PSD area, which is easy to measure with the PreAZ area that is much less certain to outline?

As stated in material and Methods both the pre- and postsynaptic densities are not defined by placing a closed contour in both densities because one can’t be certain that the dense accumulation of particles defining both areas since the impregnation (staining) and contrast of both structures critically depends on the uranyl and lead staining which could led to misinterpretation due to different staining results. That’s why we have drawn a contour line from the beginning to the end of the presynaptic density and extrapolated that for the postsynaptic density (for details see Material and Methods). In our samples both the pre- and postsynaptic densities were always clearly visible in those boutons further analyze.

Page 26 Line 640 vesicle density measurement: All the synaptic vesicles that are in the 50 nm thick section in their entirety are missed, and there are methods based on EM tomography to correct these estimations. One can not assume, that the error caused by "double counts" of vesicles cancels for the lost ones. There are stereological methods to estimate both types of error please include them and correct the values.

We would like to point out that the whole body of our work to structural analysis of vesicle pools is based on image data stemming from transmission electron microscopy (TEM) generating a projection of the entire volume of the ultra-thin section and NOT from scanning electron microscopy (SEM) where only a small volume close to the surface of the section would be captured. Operating in TEM mode ensures that no vesicle is missed only because it is embedded in its entirety in the section as postulated by the reviewer. Hence, EM tomography, which is basically a TEM operating from different incident angles in relation to the specimen or section, does not provide any advantage in detecting these vesicles. It does, however, help to better position a 3D object within the section volume itself and therefore allows to detect objects that could overlap from one viewing angle by using another angle. As the average vesicle diameter is of similar size compared to the section thickness, the possibility of a complete overlap to happen, however, is almost zero. And as we only count clear ring-like structures, a stereological correction factor calculated according to Abercrombie (1946) would underestimate real counts (see also Saetzler et al. 2002). If there is, however, relevant literature on "methods based on EM tomography" and "stereological methods to estimate both types of error" (over- and underestimates) that we are missing out on, we would appreciate the reviewer providing us with the corresponding references so that we can include such calculations in our paper.

Page 27 Line 664 and 665 "sections" are still tissue blocks, as sectioning comes after if the process is correctly written. Please correct.

We have corrected this according to the reviewer’s comment.

Page 43 Figure 4 D Data for L1b is missing, only the correlation line is visible.

Corrected in a new Figure.

Page 44 Figure 5 C arrowheads are in the correct places? Some of them do not seem to point to the edge of the synapse.

We carefully checked the Figure and adjusted the arrowheads.

Figure 5 E lower arrowhead labels something, that is difficult to identify but does not seem to be a vesicle.

We agree with the reviewer on this point and changed the figure accordingly.

Figure 5 F, the upper vesicle is at least 10 nm apart from the PreAZ membrane. Did the authors consider it as docked (indicated with arrowhead, according to the legend it labels docked vesicles)?

We agree with the reviewer on this point and changed the figure accordingly.

Page 45 Figure 6 B one of the 2 synaptic boutons (sb), sb2 has a tangential active zone that precludes the identification of the pre- and post-synaptic membranes, still 2 "docked vesicles" are labeled. How were they classified as docked? Please remove these tangential synapses from the dataset, as membranes can not be identified.

The reviewer is right that the active zone is tangentially cut, however, the two vesicles are associated with the AZ. In addition, we did not use this AZ for vesicle data analysis.

Page 46 Line 1124 interneuron axon labelled in green not brown.

Corrected as suggested by the reviewer.

Line 1129 SStC is missing.

Changed according to the reviewer’s comment.

Page 48 Table 2 Number of docked vesicles Median values are rounded to integer values? If yes why?

The statistic package used rounded to the given values.

Page 51 Supplementary Table 1 Hu_04 Histopathology, what does TLE stands for?

TLE: temporal lobe epilepsy. We included the abbreviation in the legend of Supplementary Table1, that is now table 2.

Reviewer #3 (Recommendations for the authors):

(1) Reanalysis of astrocytic coverage based on the % of synapses that form tripartite synapses.

We have reanalyzed the data concerning this point (new Figure 6D).

(2) Segregation of excitatory and inhibitory synapses.

We have now included a paragraph in our results section to distinguish between excitatory and inhibitory synapses.

(3) Better explanation of the limits of the study to assess functional parameters.

We disagree with the reviewer on this point and have not included an explanation concerning the limits of this study.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

This study uses a variety of approaches to explore the role of the cerebellum, and in particular Purkinje cells (PCs), in the development of postural control in larval zebrafish. A chemogenetic approach is used to either ablate PCs or disrupt their normal activity and a powerful, high-throughput behavioural tracking system then enables quantitative assessment of swim kinematics. Using this strategy, convincing evidence is presented that PCs are required for normal postural control in the pitch axis. Calcium imaging further shows that PCs encode tilt direction. Evidence is also presented that suggests the role of the cerebellum changes over the course of early development, although this claim is rather less robust in the current version of the paper. Finally, the authors build on their prior work showing that both axial muscles and pectoral fins contribute to "climbs" and show evidence that suggests PCs are required for correct engagement of the fins during this behaviour. Overall, establishing a role for the cerebellum in postural control is not very surprising. However, a clear motivation of this study was to establish a robust experimental platform to investigate the changing role of cerebellar circuits in the development of postural control in the highly experimentally accessible zebrafish larvae, and in this regard, the authors have certainly succeeded.

Overall, I consider this an excellent paper, with some room for improvement in aspects of presentation, discussion, and some aspects of the data analysis..

We thank the reviewer for their kind comments and support. In the revision we have addressed their concerns regarding data presentation and analysis. Additionally, we have expanded our introduction and discussion to address questions of presentation.  

Reviewer #2 (Public Review):

Summary:

Franziska Auer et al. investigate the role of cerebellar Purkinje cells in controlling posture in larval zebrafish using the chemogenetic tool TRPV1/capsaicin to bidirectionally manipulate (i.e., activate or ablate) these cells. This tool has been developed for zebrafish previously but has not been applied to Purkinje cells.

High-throughput behavioral experiments are presented to monitor how body posture is affected by these perturbations. The analysis of postural control focuses on a specific subaspect of posture: the body tilt-angle relative to horizontal just before a swim bout is executed, quantified separately for pre-ascent and pre-dive bouts. They report a broad bimodal distribution of pre-ascent bout posture ranging from -20 to +40 degrees, while the pre-dive bout posture was more Gaussian, ranging between -40 and 0 degrees. The treatment effect is quantified as the change in the median of these distributions.

Purkinje cell activation and ablation in 7 days post-fertilization (dpf) fish shifted the median of the ascending bout posture distributions to positive values. The authors hypothesize that the stochastic nature of the activation process might desynchronize Purkinje cell activity, thus abolishing Purkinje cells' role in postural control, similar to ablation. However, this does not explain why dive bout posture decreased upon activation but was unaffected by ablation. 

To test whether the role of Purkinje cells in postural control matures over development, the authors repeated the ablation experiments at 14 dpf. They state that "at 14 dpf, the effects of Purkinje cell lesions on posture were more widespread than at 7 dpf." However, this effect size is comparable to that observed at 7 dpf, suggesting no further maturation of the role of Purkinje cells in pre-ascending bout postural control. The median pre-dive bout posture decreased at 14 dpf, contrasting with no effect at 7 dpf, yet this change was comparable in effect size to the activation effect on Purkinje cells at 7 dpf. The current data breadth may not be sufficient to conclude that signatures of emerging cerebellar control of posture across early development were uncovered.

The study's exploration of activating Purkinje cells in freely swimming fish using TRPV1/ capsaicin is of special interest, but the practicability of this method is unclear from the current presentation. It would be beneficial to present the distribution of the percentage of activatable Purkinje cells across animals and time points to provide insight into the method's efficiency. Discussing this limitation and potential improvements would aid in evaluating the method, especially since the authors report that the activation experiments were labor-intensive, limiting repeat experiments. This may explain why the activation experiment at 7 dpf is the only data presented with cell activation, with other analyses performed using the cell ablation capabilities of the TRPV1/capsaicin method.

Another data point at 14dpf would significantly strengthen the conclusions.

The authors analyze Purkinje cell-controlled fin-trunk coordination by examining ascending bout posture across different swim bout speeds. They make the important finding that pectoral fin movements contribute significant lift for median and fast swim bouts but not for slow ones, and that Purkinje cell ablation disrupts lift generation at all speeds.

Finally, the authors examined whether Purkinje cell activity encodes postural tilt-angle by performing calcium imaging on 31 cells from 8 fish using their Tilt In Place Microscope (TIPM). They report that they could decode the tilt-angle from individual neurons with a highly tuned response, and also from neurons that were not obviously tuned when pooling them and analyzing the population response. However, due to the non-simultaneous recordings across animals, definitive conclusions about populationlevel encoding should be made cautiously, it might be better to suggest potential population encoding that needs confirmation with more targeted experiments involving simultaneous recordings.

Strengths:

- The study introduces a novel application of the chemogenetic tool TRPV1/capsaicin to study cerebellar function in zebrafish.

- High-throughput behavioral experiments provide detailed analysis of postural control.

- The further investigation of Purkinje cell-controlled fin-trunk coordination offers new insights into motor control mechanisms.

- The use of calcium imaging to decode postural tilt-angle from Purkinje cell activity presents interesting preliminary results on neuronal population encoding.

Weaknesses:

- The term "disruption" for postural control effects may lead to misleading expectations.

- The supporting data show only subtle median shifts in postural angle, raising questions about the significance of observed effects. Statistical methods that account for the hierarchical structure of the data might be required to support the conclusions.

- The study's data breadth may not be sufficient to conclude emerging cerebellar postural control across early development.

- The current presentation does not adequately detail the practicability and efficiency of the TRPV1/capsaicin method for activating Purkinje cells, and the labor-intensive nature of these experiments constrains the ability to replicate and validate the findings.

- Non-simultaneous recordings in calcium imaging necessitate cautious interpretation of population-level encoding results.

We appreciate the reviewer's thoughtful and detailed feedback. In response, we have made several changes to highlight key points in our manuscript. We have adjusted our wording to more accurately reflect the scope of our findings. Finally, we have clarified and expanded the methods used.

Reviewer #3 (Public Review):

Summary:

This paper uses a new chemogenetic tool to investigate the role of cerebellar Purkinje cells in postural control. Using a high-throughput behavioral assay, they show that activation or ablation of Purkinje cells affects various aspects of postural control in zebrafish larvae during spontaneous swimming and that the effects are more pronounced at later developmental time points, where the Purkinje cell number is much greater. Using a sophisticated imaging assay, they record Purkinje cell activity in response to the tilt of the fish and show that some Purkinje cells are tuned to tilt direction and that the direction can even be decoded from untuned neurons.

Strengths:

Overall the study is nice, using a range of tools to address a fundamental question about the role of the cerebellum in postural control in fish.

Weaknesses:

(1) The data in Figure 1 that establishes the method seems to be based on a very small number of experiments and lacks some statistical analysis.

(2) The choice and presentation of the statistical and analysis methods used in Figures 2-5 could be improved.

We thank the reviewer for their comments.  We have added additional statistical analyses for the activation experiments, and improved data presentation .

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Overall I think this is a great paper.

* Introduction and Discussion.

The Introduction (and Discussion) do little to explain what is understood about cerebellar control of posture and what major outstanding questions remain. The first paragraph of the Introduction seems to argue that the role of the cerebellum in control of posture is well established and line 24 attempts to motivate the present study by virtue of the fact that terrestrial locomotion is "complex". This might be true but is not necessarily a major obstacle given the suite of powerful approaches available in rodent neuroscience. What are the major challenges that are hard to tackle in rodents and what specific questions can the larval zebrafish help to answer? What about development (which gets no mention at all)? I'm not suggesting a comprehensive review of every aspect of cerebellar physiology, but I think the Introduction should attempt to outline the current hypotheses in a little more detail and highlight what we still need to understand.

We take the Reviewer’s point that there is more to say in the Introduction. We feel that multi-dimensional limb biomechanics and proprioception are two aspects of terrestrial locomotion that support our use of the word “complexity.” However, we don’t dwell on this point because, as the reviewer correctly states, the suite of tools for rodent neuroscience & behavior is expansive and, in our opinion, not a limiting factor. Instead, we said what we felt we could regarding the potential contribution of the larval zebrafish in the last paragraph of the Discussion. In the revision, we have added details about the development of cerebellum to the introduction (though this, of course, is an expansive topic and well-beyond the scope of the Introduction), highlighted some of the historical limitations in rodent posture analysis, and set up the .

* Figure 2: 'Arrows denote the shift towards more nose-up postures'. I think the distribution is quite easy to interpret without these arrows; I suggest removing them.

We have removed the arrows.  

* IQR is sometimes stated as a single number and sometimes as a range. It should be consistent and unless eLife has guidance to the contrary, I suggest that it be the latter.

Thank you for pointing that out. We now report it as the value at the 25&75th %ile for all IQRs.  

* Figure S2: For 14 dpf fish the axes are labelled PC2/3 - is this an error?

We have changed it to a 3-dimensional plot for both 7 and 14 dpf data to show comparable plots for both ages (now Figure S5 F and G). For the analysis in the 14dpf fish the clearest separation was in the space defined by the 2nd and 3rd principal component.  

* In the methods, there is insufficient detail given about fluorescent imaging.

We added additional information to how the fluorescent imaging was performed to the ‘Confocal imaging’ section as well as to the ‘Functional imaging section’

* Abstract

In my opinion, the statement "Here, we used a powerful chemogenetic tool (TRPV1/ capsaicin) to *define the role of Purkinje cells*..." is too strong. Whilst the evidence that PCs are required for postural control is certainly strong, what exactly these cells do in the service of postural control is far from clear (as the authors indeed acknowledge in the Discussion). As such, I wouldn't say their role has been "defined".

We change the word to “describe” to better reflect our findings

* aldoca transgenic.

This appears to be a beautiful transgenic line but the data showing the extent of its expression and evidence that in the cerebellum it exclusively labels PCs isn't clear enough.

(i) Ideally Figure 1A would show an image of a whole animal to provide an overview of transgene expression but instead it seems to be (the legend is unclear) a cartoon with a confocal projection of part of the brain overlaid.

We have updated the figure legend to be clearer that we show a cartoon of a larval zebrafish with the confocal image overlaid. The aldoca promotor has been previously described and exclusively labels Purkinje cells (10.1523/JNEUROSCI.3352-10.2010)

(ii) Figure 1B shows expression in the cerebellum, but how are we to understand that all the labelled cells are PCs? Are all PCs labelled, or only a subset? Perhaps a double labelling with a PC in situ marker could be done to demonstrate colocalisation?

As above, the aldoca promotor has been previously described; to the best of our knowledge in the Hibi lab’s hands (and ours) it labels Purkinje cells exclusively, and it labels all of them (10.1523/JNEUROSCI.3352-10.2010)  

* Chemogenetic validation.

Overall, the chemogenetic approach to abrogate PC function looks to be very powerful. The authors state in several places that a contribution of this paper is in its "establishing the validity of TRPV1/capsaicin-mediated perturbations". However, the data in Figure 1, along with various comments in other parts of the paper raise some questions:

(i) For experiments depolarising PCs with 1µM CSn, the same size is tiny: Two transgenic animals and one control. Moreover, it is stated 'in one fish ... we observed a small number of neurons at the 9h timepoint with bright, speckled fluorescence suggestive of cell death". Was this one out of two transgenics?! In the discussion, I didn't understand the statement "ensure adequate brightness levels *to achieve sufficient depolarization without excitotoxicity*". Does this "excitotoxicity" relate to the specked fluorescence observation?

Overall, the very small sample size and comments about excitotoxicity and cell death raise concerns about the approach that I think warrant clearer treatment in the results (including information about the assessment of transgene expression, % embryos judged to have suitable expression), especially as this paper is seeking to establish the validity of the method.

We note first that the method has been previously validated (https://doi.org/10.1038/ nmeth.3691) and that we build on this work. For the experiment described, the point was to identify an acceptable duration for exposure. To that end, we analyzed 6 animals for up to 6h (including the washout experiments in Figure S1B) where we never observed any speckled fluorescence; we limited our behavioral experiments to 6h accordingly. We thought it would be worth including the observation of speckled fluorescence at 9h timepoint for future reference. To directly address the comment we have increased the number of analyzed cells and fish for the 1uM capsaicin experiments and added statistical analysis (lines 65-67).

When screening for transgene expression we selected for fish that had clearly visible expression, but that did not look overly bright, and used the same criteria when screening fish for the GCaMP imaging and for behavior. Around a quarter of the fish that had aldoca:TRPV1-tagRFP expression had a usable expression level for the activation experiment. We have added this information to the Results (line 62) and Methods (line 369-372)

(ii) The authors note "capsaicin could sporadically activate subsets of Purkinje cells" and further speculate about PC activity and synchrony in the discussion. Figure 1 seems to rely on single images at widely spaced time points but given that they are set up to do 2-photon calcium imaging, why didn't they collect continuous time series data and analyse the temporal patterns of activity across the transgenic PC population?

We have added time series data for calcium imaging after 1uM of Capsaicin in TRPV1-  and TRPV1+ cells to Supplementary Figure S1A. Here too we see sporadic increases in calcium levels at similar rates: 0% for TRPV1- and 15-19% for TRPV1+ (see also Figure S1 legend)

(iii) The axonopathy and cell death resulting from 10 µM Csn is quite dramatic.

However, here the authors do not appear to have included a TRPV1 negative control (although oddly they did for 1 µM treatment) so it is currently unclear whether or not a high conc of Csn alone might be cytotoxic.

Chen et al (https://doi.org/10.1038/nmeth.3691) have established the TRPV1/capsaicin method in zebrafish with broad neuronal label and did not see any effect with high doses of capsaicin in TRPV1 negative fish.  

* Behavioural assessment - stats

Overall, the disruption of postural stability after PC manipulations is convincing.

However, I have a few queries about the statistics:

(i) In this section, the statistical unit was not clear. The tables, which are otherwise very useful, give no indication of N. The legend text does report "8 repeats/149 control fish" and "across experimental repeats" suggesting the statistical unit might be the repeats rather than animals, but this should be clarified. In Figure 2G, individual data points should be plotted if N=8, or a representation of the distribution (eg violin or box and whisker plots) if N = 149.

We apologize for the confusion. Given the variable numbers of bouts, a single experimental repeat does not allow for an accurate estimate of expected value. Below we simulated how accurately the median can be estimated based on increasing sample sizes (Author response image 1). Given that large numbers of bouts are necessary to accurately estimate the median we pool the data for all experiments and use resampling statistics to estimate bias in our estimate.

Author response image 1.

Median estimation based on increasing sample size

(ii) Related to the above, I hope it might be easier to interpret the unexpected change in climb posture in ablation controls once the data for individual repeats is shown.

When we analyze the data as single repeats we see considerable variability between different repeats due to undersampling. We tested the medians for the single repeats for outliers to ensure that the shift is not due to a single repeat skewing the distribution. We did not detect any outliers in the pre-lesion control or in the post-lesion control group. (Outliers were determined as deviating more than 3 times the scaled median absolute deviation (MAD) from the median. A scaling factor of 1.4826 was used to ensure that MAD-based outlier detection is consistent with other methods like Z-scores.) We added this information to line 133-134 and the method section under Statistics. 

(iii) In some parts of this section, including the Tables, the authors report the 95% CI of the median, rather than IQR. In this case, they should report the z-value used for 95% CI estimation.

As we are using resampling to estimate the 95% confidence interval of the median there is no z-value as in a traditional normal distribution based confidence interval; Instead, we explicitly define the 2.5th and 97.5th percentiles from the bootstrapped sample distribution, which captures the middle 95% of the data, representing the 95% confidence interval.

* It is stated that "fish adopted more nose-up postures before *and throughout* climb bouts". Figure 2F seems to show posture before the climb, but where is the "throughout" data? It would be useful if Figure 2E, J could be extended to make a bit clearer these two phases of postural assessment.

We removed the phrase ‘throughout climb bouts’ as we are not showing the posture throughout the bout and to avoid over complicating the interpretation.  

* Why were PCs not activated at 14 dpf (eg using 1 µM Csn)?

Due to shifts in priorities the first author will not be continuing this series of experiments, and so this additional experiment will have to wait for someone to pick up this line of inquiry

* The authors appear to claim that the difference in phenotype in 7 versus 14 dpf animals following high conc Csn treatment is indicative of a changing role for cerebellar PCs over this developmental period. For instance, in reference to the 14 dpf ablation phenotype, the authors write "reveals the functional emergence of Purkinje cell control of dives" and in the abstract they talk about "emerging control of posture across early development". However, can they rule out that the phenotypic differences might instead reflect differential sensitivity of the relevant PC (sub)populations to CSn at the two ages? If this caveat cannot be discounted then I suggest it is acknowledged e.g. in the discussion.

As previously established, all Purkinje cells are labeled in the aldoca line (10.1523/ JNEUROSCI.3352-10.2010). Fluorescence is brighter at 14dpf compared to 7dpf, suggesting higher levels of TRPV1. We therefore assume that at 14 dpf, the high concentration of Csn is sufficient to ablate Purkinje cells. At 14 dpf, cerebellar damage is visible under a standard dissecting microscope.The preponderance of evidence therefore speaks against a previously undiscovered subpopulation of TRPV1expressing Purkinje cells that are, by mechanisms yet unknown, resistant to high doses of capsaicin. 

* Fin-body "coordination"

The ideas and data around fin-body coordination are very intriguing.

(i) The statement "fin engagement is speed-dependent" would benefit from a stats test to show this is indeed significant. The data in Figure 4B suggest a rather high degree of variance.

This is an important point; we appreciate the Reviewer’s attention. We have added statistics to show this is speed dependent to line 167-169 and show the corresponding plot in the supplement in Figure S4.  "Here, we observed that fin engagement is speeddependent, with faster bouts producing greater lift for a given axial rotation (Spearman correlation coefficient: control 0.2193; 10uM capsaicin: 0.0397; Z-test after ztransformation: p < 0.001)  

(ii) The statement "After capsaicin exposure, the slopes of the medium fast speed bins were significantly lower (Figure 4C), reflecting *a loss of speed-dependent modulation*" is not convincing. The slope is likely a function of both speed and Csn treatment, and the comparisons in Figure 4C appear to be testing the latter, not the former.

We understand the reviewer’s point. However, the slope for the slow bouts remains unchanged. We therefore conclude that the reduction in fin-body slope is speed dependent and not a speed independent reduction of slope overall. 

We have made this more clear by adding Supplementary Figure S4 and changing the text in line 177-179. 

(iii) I'd like to understand more about the phenotype of the fin-amputated animals. Were any "bout" parameters changed? Did the animals still attempt climbs and was the distribution of the upward rotation parameter similar to controls? The text states "the slope of the relationship between upward rotation and lift was indistinguishable from zero" but the stats reported in the text are comparisons between groups while Table 5 shows 95% CIs that don't span zero. Some clarification would be useful here.

We appreciate the Reviewer’s interest. We’ve studied climbing in fin-amputated animals at length here: https://doi.org/10.7554/eLife.45839 and here: https://doi.org/10.1016/ j.celrep.2023.112573 and have added these references in line 183.

(iv) The authors repeatedly refer to fin-body *coordination* but it is not clear whether the loss of lift after PC ablation is a result of an explicit coordination defect (i.e. changes in the relative timing and/or kinematics between fins and axial motion components), versus a simple reduction in pectoral fin engagement. Either result could be interesting, but this should be clarified.

Thank you for pointing that out. In the fastest speed bin, we observed an increase in upward rotation and a decrease in average fin lift. In contrast, the medium speed bin showed no significant changes in average fin lift or upward rotation (see Author response image 2 and Tables 4 and 5), yet already displayed coordination deficits. Based on these observations, we argue that Purkinje cell lesions primarily affect coordination, rather than simply reducing one specific parameter such as lift or rotation (line 293-298).

We have added fin lift and rotation values from Author response image 2 for all speed bins to tables 4 and 5.  

Author response image 2.

Fin lift and rotation for slow, medium and fast bouts

* PC activity and decoding of pitch direction.

The clever TIPM method is used to collect calcium data that convincingly shows that individual PCs can encode pitch-tilt direction. However, a population of "not tuned" cells are also identified, and here I found the analysis of their responses and the argument that they encode pitch direction at a population level difficult to follow.

(i) First, although the naming of the cells implies that individual neurons do not encode pitch direction, I did not find this convincing. Figures 5F/G suggest that several "not tuned" cells in fact show quite consistent differences in activity across trial types and indeed in terms of their average responses sit as far from the unity line as do several "tuned" cells.

The Reviewer’s comment helped us clarify some key points. First, tuned and untuned cells were categorized based on a Directionality Index threshold of 0.35; some cells might look similar in 5F/G but the highly variable responses of Purkinje cells have highly variable response so overall there was no consistent tuning. We have clarified this in the text in line 203-207 Below we have plotted the Up versus Down responses for the 10 least tuned cells (sorted by directionality index). While some cells have higher responses on average to one direction we think that the variability makes it difficult to support a claim for “tuning.” We have also tested the support vector machine on the least tuned cells to confirm that the chosen cutoff for tuned/untuned is not affecting our claim that untuned cells can encode position.(see also Author response image 4)

Author response image 3.

Trial-by-trial variability

(ii) It is therefore not very surprising that PCA (and the SVM decoder) distinguishes trial type. I would guess that PCA assigns the largest weights to these most tuned of the "not tuned" cells, and the 3-5 cell decoders do well when these cells happen to be sampled.

Author response image 4.

Decoding accuracy of the 3/5/7 least tuned cells

This was an interesting idea. To rule out that it is only the most tuned cells that contain the information, we tested the decoder on the 3/5/7 least tuned cells; here too, 5 and more cells are better able to accurately decode the direction. We have add the decoding accuracy to the text in line 221-224

(iii) As I understand the analysis, Figure 5G shows responses for "not tuned" cells over 21 trials (of each type) but these are not the same trials for the different cells? How then is population coding being assessed?

We have updated the text and refer to this data as a “pseudo-population” in lines 216 and 218 for all experiments where we combined cells from different fish. For technical reasons, when we perform TIPM at eccentric angles we must use sparsely labelled fish to ensure that we can find the same cells over a 60 degree range. We have repeated our analyses for TIPM centered at the horizon, where we can record from entire populations from a single fish.  

(iv) Furthermore, Figure S2 shows a somewhat different analysis with decoding accuracy measured on a fish-by-fish basis. In this case, are these decoders for simultaneously imaged neurons? Is this a cross-validated measure of decoding accuracy?

Yes, as above, Figure S4 (former S2) looks at fish-by-fish basis of simultaneous recorded neurons. Yes, it was 5-fold cross validated. We have updated the text in line 490-494.

Reviewer #2 (Recommendations For The Authors):

- Postural control involves various aspects such as balance, coordination, relative body part orientations, and stability. Discussing these and presenting in this context the specific subaspect characterized in this study would help clarify which aspect of postural control the work focuses on.

The Reviewer makes an interesting point, but we think their description of what constitutes postural control is overly broad. Specifically, control of “relative body part orientations in space” by definition requires coordination, and subserves balance and stability. We acknowledge, of course, that different aspects can be and often are treated independently. While interesting, a full treatment of what comprises “postural control” is beyond the scope of the paper, as it would require reconciling the terms across taxa, effectors, environments and well over a century of experiments.

We contend that posture — particularly underwater — is best defined as the relative orientation of body parts in space. For fish, those parts consist of predominantly axial muscles and secondarily fins. We present these definitions in the Introduction and thank the Reviewer for encouraging us to more clearly shape our findings.

- Disruption of posture or postural control: The use of the word "disruption" could lead to misleading expectations. While it may not be incorrect, it suggests a significant loss of equilibrium, an obvious increase in postural variability, or at least a noticeable effect when observing an individual animal's behavior. However, the supporting data show only a subtle median shift in postural angle within a very broad distribution averaged over many individuals. This effect was only significant when comparing fish with a control group, not when comparing fish posture before and after the treatment.

Replacing "disruption" with "modification" would be more cautious.

We take the Reviewer’s point and have adjusted our wording to "modifies postural control.” In lines 137, 266, and 283

- Statistical significance: Consider aligning the asterisk notation with conventional standards (e.g., * for p < 0.05, ** for p < 0.01, *** for p < 0.001) to enhance clarity for readers. On the other hand, the individual measurements might not be independent (e.g., measurements from the same fish, or the same tank are likely to be correlated), so using the Wilcoxon rank-sum test (Mann-Whitney U test) on pooled data might lead to incorrect conclusions. Methods that account for the hierarchical structure of the data might be required to support the conclusions.

We take the Reviewer’s point about the importance of conventions, however we have never found “more stars = more significant” to be all that helpful in evaluating claims. Instead, we’ve opted to have both a significance and effect size criteria; a “star” here reflects our considered confidence in the difference we observe. 

We agree that the hierarchical nature of pooled data is worth considering/presenting.

We performed a two-way analysis of variance (ANOVA) on the interquartile ranges (IQRs) of the single experimental repeats for the 7 days post-fertilization (dpf) activation, 7dpf lesion, and 14dpf lesion experiments. The ANOVA revealed no significant main effects, supporting the strategy of pooling experimental repeats to estimate distributions.

The results of the ANOVA, along with the IQRs for all experimental repeats, are presented in Tables 6-11. We have also clarified this in the methods section in lines 505-509.

- Data representation: All data of postural angles should be represented in the form of violin plots to show the underlying distributions of the postural angles, especially given that the effect size is small relative to the dispersion of the distribution of the postural angle and that this distribution is also not Gaussian but bimodal, and different before and after the treatments.

We take the Reviewer’s point that seeing the full distribution can be useful. We have added plots of the raw distributions for the data in Figure 3 as supplemental Figure S3.

- Showing the distributions will provide the necessary information for the reader to evaluate the importance of the effect. For all data shown in Table 1, the distributions should be presented in the supplementary information.

As requested, we have added the distributions of the data in Table 1 to the supplement (Figure S2)

- Roll posture: A statement about whether roll posture is perturbed by Purkinje cell manipulation would be a piece of important additional information helping to understand how strong the 'disruption' of posture is.

We haven’t assessed roll posture, as this is not practical in the current version of the SAMPL apparatus. We have added this limitation to the results (line 116) but also note that as our manipulations are bilateral, we don’t anticipate any systematic changes to roll.   

- Comparison with other methods: Add a discussion on how the TRPV1/capsaicin method compares with other methods, such as using nitroreductase (Ntr) for targeted pharmaco-genetic ablation of cells by treatment with metronidazole or the the possibility to to ablate Purkinje cells by KillerRed as the author lab has done previously. Both methods have been applied to ablate Purkinje cells in larval zebrafish. What are the advantages of the TRPV1 method compared to these when neglecting the activation possibility?

Thank you for that suggestion, we have added a section to the discussion where we compare the TRPV1/capsaicin lesion to other lesion methods (lines 334-336)

- Describe the decoding algorithm: The decoding algorithm used could be described more in detail in the methods section.

We have described the decoding algorithm in more detail in the methods under ‘Functional GCaMP imaging in Purkinje cells.’ Line 488+ 

We used a support vector machine (SVM) with a linear kernel. The SVM model was trained using k-fold cross-validation, which splits the data into k subsets (folds). At each iteration, the model was trained on k-1 folds and tested on the remaining fold, ensuring that the model performance was evaluated on unseen data in each fold. Permutations were performed on randomized trial identity as a null hypothesis (5-fold cross-validation; 100 shuffles for randomization). Accuracy was calculated as 1 minus the classification loss.  

- Availability of code: The link to the data and code repository is not working.

Thank you for pointing that out, we have fixed it now. In the lower right of the page you can see the history of all changes to the repository, including the entry on 2023-09-08 where the corresponding author set it to “public.” When we checked thanks to your comment, it had been set to “private,” without any record of when/why. We have reset it 2024-10-17. We will continue to check it periodically in the future and apologize in advance if it is unavailable; this is the first time we’ve seen that happen.

- Electrophysiological Control: Including an electrophysiological characterization of the activation of Purkinje cells by the TRPV1/capsaicin would significantly strengthen the validity of the method.

We take the Reviewer’s point that electrophysiological characterization is a way to strengthen the validity of the method. However, Chen et al (h"ps://doi.org/10.1038/ nmeth.3691) have performed electrophysiology during neuronal activation and concluded that TRPV1 activation with capsaicin indeed increases neuronal activity and firing rates increased. Our calcium imaging and lesion experiments amply demonstrate that Purkinje cells are sensitive to TRPV1-mediated currents. We therefore do not believe that the additional information gained by arduous electrophysiological evaluation is merited here.

- Describe more in detail how climb and dive bouts are defined. The height difference between consecutive bouts measured 250ms before the bout of executions.

Climb and Dive bouts are split by the angle of their trajectory. If the fish moves up (i.e. trajectory larger 0) it is considered a climb bout and vice versa for dive bouts. 250ms prior to the maximum speed is roughly the time the fish initiate a bout, so the pre-bout posture is measured when at this point. The time-courses of bouts are dissected extensively in Zhu et. al. 2023. We have added a definition for climb and dive bouts to the method section under ‘Behavior analysis’ line 453 and 454.  

- Figure 1H: Why can't you ablate all Purkinje cells but only about 80%?

This is an excellent question. We opted for an extremely conservative count, and included everything that was still resembling a cell, even if it might not be functional/ already dying. Our counts are therefore likely an underestimate of the percentage of cells that were lost. We have added this point to the text in lines 393 395

- Figure 2C: The method is not fully clear. At 8dpf 0.1uM capsaicin is added to the chamber. At what time after the application of capsaicin did the behavioral recording start?

We recorded after about 10-15min after adding the 1uM Csn to the chambers. The fish were fed after the 6h in capsaicin. We have added this information to the method section line 404 - 408.

- Figure 2F: What indicates the shown confidence interval? Also median with a 95% confidence interval calculated over the experiments in parallel?

The distributions shown in Figure 2F take data from all experiments pooled. We use resampling methods to determine the variability in our estimates. The distribution plots are showing the median and the 25th and 75th percentile of the resampled distribution. We have added this information to the figure legends.

- Figure 3: Subtitles on panel D and E indicating <climb bout posture> and would facilitate reading.

We have added the subtitles to those panels.

- Figure 4: Describe in the methods how recordings from individual fish were mapped onto each other to superimpose the Purkinje cell locations recorded from the 8 fish.

We have added the respective section to the methods: Line 481 - 483

“To map the anatomical locations of the recorded cells, we imaged overview stacks for each fish. These stacks were manually aligned in Illustrator, and the cells included in the analysis were reidentified and color-coded according to their tuning properties.”

Reviewer #3 (Recommendations For The Authors):

Major points:

(1) Lines 74-81. The data presented here and in later experiments to argue for an effect of capsaicin on neural activity lacks statistical rigor because of the apparently very small numbers of animals/cells assessed. For example, the control appears to involve 4 cells assessed from 1 animal, and the experimental group is just 2 animals. Given that the interpretation of the paper depends upon this result, it is worthwhile to show the result more clearly, and with some statistical analysis. They argue in the discussion that "Our imaging assay established that 1 µM of capsaicin would stochastically activate subsets of Purkinje cells" which seems a stretch from the data as presented.

We appreciate this point, which was shared by Reviewer 1. We have added more data and performed statistical analysis (line 63 - 67 as well as Figure S1A)

(2) I found the practice of sorting effects by a mixture of effect size and p-value to be a little arbitrary, although in this case, it seems likely that it identified the most relevant effects. I would have preferred to see some attempt to correct for multiple comparisons (e.g. by resampling with the identities of fish shuffled to estimate the distribution of each measurement for this population size), followed by filtering for effect size after establishing a corrected threshold for significance.

We take the Reviewer’s point, though we note that critical values for effect size and pvalue are inevitably “a little arbitrary.” We can’t do the exact analysis the Reviewer suggests as we do not measure data from individual fish for these experiments. However, we did calculate new critical p-values (added to the Tables) that account for multiple comparisons using Šidák’s method.

(3) Figure 4. The data here is a little strange in that the slope in the control condition for medium speed is given as much larger than for slow, but the data in the two cases appears largely overlapping for most of the range of behavior, only diverging for the most extreme rotations. It seems perhaps that the measurement of slope is strongly dependent on these most extreme values. The authors might want to consider the use of robust regression methods which might mitigate these effects.

This is an interesting observation and we appreciate the Reviewer’s thoughtful suggestion. We now use a robust regression method (bisquare weighting of residuals).

We have adjusted all values in lines 175 - 177  and added the regression method to the Methods section line 520.

(4) Figure 5. The 'principal component analysis' description is extremely unclear. The text says that PCA 'showed near-complete segregation of trial types' but it is not explained how this was achieved with PCA or how this was quantified. Figure panels show the data plotted using different pairs of PCs showing visual evidence of segregation. In the methods, it is stated that "We performed principal component analysis" and that "cells were used for principal component analysis and subsequent support vector machine decoding analysis". What is meant exactly by 'performed PCA'? Was PCA used in a dimensionality reduction step? And if so, how many and which PCs were chosen and why? For visualization of the separation, the authors show arbitrary pairs of PCs. Could it be better to use a method more suited to that purpose such as linear discriminant analysis?

PCA was used to define a subspace to qualitatively evaluate if different trials could be separated. Once it became clear that it could, we next trained a binary decoder on the complete dataset (i.e. no dimensionality reduction). We did not perform linear discriminant analysis as the unsupervised PCA already showed separation of trial types.  We have made this clearer in lines 212 - 214.

(5) Why does the decoding analysis use only untuned cells? Isn't it equally, or more, interesting to know how well tilt can be encoded using all cells? It is unclear to me what we learn by selecting only untuned cells for this analysis (although I agree it is interesting that this does work).

We focused exclusively on untuned cells because including even a single highly tuned cell for the population coding will lead to excellent results. By using untuned cells we test if there is some directionality information that is not visible just by looking at the up/ down responses of single cells. We have made this clear in lines 217 - 218

Minor points and corrections:

(1) Maybe consider losing the words 'powerful' (I think it is overused and not well defined) and 'reagent'. Reagent is normally used for something that participates in a reaction. It is a bit odd to use it to refer to a transgenic animal. Later it is called a 'tool' which seems better.

We have changed the wording and refer to it as tool for the whole paper.  

(2) Figure 1D. Please use a color bar to indicate the scale.

We have added a color scale to the panel

(3) Saying that 'posture' increases is confusing, although the meaning can be inferred from the overall context and the definitions in the Methods - could Posture be capitalized to indicate a specific definition is being used rather than the general meaning?

This suggestion agrees with those made by Reviewer 2. We have changed the wording to “postural angle.” 

(4) The arrowheads in Figure 2FHK are unnecessary and confusing (why are some horizontal and some vertical?).

Thank you for that suggestion, we have removed the arrowheads.

(5) Figure 3 The legend should indicate that the image is shown with an inverted lookup table.

We have updated the legend

(6) Figure 3 D and E Titles would be helpful, so it is not necessary to refer to the legend to understand the difference.

We have added titles to the figure panels

(7) The dwell time for the 2-photon experiments is given in the manuscript, but I think the authors meant microseconds?

Thank you for pointing that out. We have corrected it to microseconds.

I haven't had much interaction with administrators as far as talking about the use of Ai, but I think that it definitely shows with the fact that it is so available to students even on UVU cites. Most teachers has a positive attitude about it, but the use of it has obviously be discussed a lot.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors investigate the effects of aging on auditory system performance in understanding temporal fine structure (TFS), using both behavioral assessments and physiological recordings from the auditory periphery, specifically at the level of the auditory nerve. This dual approach aims to enhance understanding of the mechanisms underlying observed behavioral outcomes. The results indicate that aged animals exhibit deficits in behavioral tasks for distinguishing between harmonic and inharmonic sounds, which is a standard test for TFS coding. However, neural responses at the auditory nerve level do not show significant differences when compared to those in young, normal-hearing animals. The authors suggest that these behavioral deficits in aged animals are likely attributable to dysfunctions in the central auditory system, potentially as a consequence of aging. To further investigate this hypothesis, the study includes an animal group with selective synaptic loss between inner hair cells and auditory nerve fibers, a condition known as cochlear synaptopathy (CS). CS is a pathology associated with aging and is thought to be an early indicator of hearing impairment. Interestingly, animals with selective CS showed physiological and behavioral TFS coding similar to that of the young normal-hearing group, contrasting with the aged group's deficits. Despite histological evidence of significant synaptic loss in the CS group, the study concludes that CS does not appear to affect TFS coding, either behaviorally or physiologically.

We agree with the reviewer’s summary.

Strengths:

This study addresses a critical health concern, enhancing our understanding of mechanisms underlying age-related difficulties in speech intelligibility, even when audiometric thresholds are within normal limits. A major strength of this work is the comprehensive approach, integrating behavioral assessments, auditory nerve (AN) physiology, and histology within the same animal subjects. This approach enhances understanding of the mechanisms underlying the behavioral outcomes and provides confidence in the actual occurrence of synapse loss and its effects. The study carefully manages controlled conditions by including five distinct groups: young normal-hearing animals, aged animals, animals with CS induced through low and high doses, and a sham surgery group. This careful setup strengthens the study's reliability and allows for meaningful comparisons across conditions. Overall, the manuscript is well-structured, with clear and accessible writing that facilitates comprehension of complex concepts.

Weaknesses:

The stimulus and task employed in this study are very helpful for behavioral research, and using the same stimulus setup for physiology is advantageous for mechanistic comparisons. However, I have some concerns about the limitations in auditory nerve (AN) physiology. Due to practical constraints, it is not feasible to record from a large enough population of fibers that covers a full range of best frequencies (BFs) and spontaneous rates (SRs) within each animal. This raises questions about how representative the physiological data are for understanding the mechanism in behavioral data. I am curious about the authors' interpretation of how this stimulus setup might influence results compared to methods used by Kale and Heinz (2010), who adjusted harmonic frequencies based on the characteristic frequency (CF) of recorded units. While, the harmonic frequencies in this study are fixed across all CFs, meaning that many AN fibers may not be tuned closely to the stimulus frequencies.

We chose the stimuli for the AN recordings to be identical to the stimuli used in the behavioral evaluation of the perceptual sensitivity. Only with this approach can we directly compare the response of the population of AN fibres with perception measured in behaviour. We will address this more clearly in the revision.

If units are not responsive to the stimulus further clarification on detecting mistuning and phase locking to TFS effects within this setup would be valuable.

It is unclear to us what the reviewer alludes to. We ask to rephrase the question.

Given the limited number of units per condition-sometimes as few as three for certain conditions - I wonder if CF-dependent variability might impact the results of the AN data in this study and discussing this factor can help with better understanding the results. While the use of the same stimuli for both behavioral and physiological recordings is understandable, a discussion on how this choice affects interpretation would be beneficial. In addition a 60 dB stimulus could saturate high spontaneous rate (HSR) AN fibers, influencing neural coding and phase-locking to TFS. Potentially separating SR groups, could help address these issues and improve interpretive clarity.

In the discussion of a revised version of the manuscript, we will point out the pros and cons of using fixed-level stimuli that were not adjusted in frequency to the BF.

A deeper discussion on the role of fiber spontaneous rate could also enhance the study. How might considering SR groups affect AN results related to TFS coding? While some statistical measures are included in the supplement, a more detailed discussion in the main text could help in interpretation. We do not think that it will be necessary to conduct any statistical analysis in addition to that already reported in the supplement.

We will consider moving some supplementary information back into the main manuscript when revising.

Although Figure S2 indicates no change in median SR, the high-dose treatment group lacks LSR fibers, suggesting a different distribution based on SR for different animal groups, as seen in similar studies on other species. A histogram of these results would be informative, as LSR fiber loss with CS-whether induced by ouabain in gerbils or noise in other animals-is well documented (e.g., Furman et al., 2013).

We will add information on the distribution when revising.

Although ouabain effects on gerbils have been explored in previous studies, since these data already seems to be recorded for the animal in this study, a brief description of changes in auditory brainstem response (ABR) thresholds, wave 1 amplitudes, and tuning curves for animals with cochlear synaptopathy (CS) in this study would be beneficial. This would confirm that ouabain selectively affects synapses without impacting outer hair cells (OHCs). For aged animals, since ABR measurements were taken, comparing hearing differences between normal and aged groups could provide insights into the pathologies besides CS in aged animals. Additionally, examining subject variability in treatment effects on hearing and how this correlates with behavior and physiology would yield valuable insights. If limited space maybe a brief clarification or inclusion in supplementary could be good enough.

We do indeed have data on ABR amplitudes and the wave 1 growth functions but only in response to broadband clicks. For more frequency-specific information, mass-potential recordings are available, obtained before and after ouabain treatment. Regarding neural tuning, we did not obtain full frequency-threshold curves but do have bandwidths for response curves recorded close to threshold. We are in the process of analyzing all these data further and will consider how to best incorporate them into the manuscript, to address the reviewer’s concerns.

Another suggestion is to discuss the potential role of MOC efferent system and effect of anesthesia in reducing efferent effects in AN recordings. This is particularly relevant for aged animals, as CS might affect LSR fibers, potentially disrupting the medial olivocochlear (MOC) efferent pathway. Anesthesia could lessen MOC activity in both young and aged animals, potentially masking efferent effects that might be present in behavioral tasks. Young gerbils with functional efferent systems might perform better behaviorally, while aged gerbils with impaired MOC function due to CS might lack this advantage. A brief discussion on this aspect could potentially enhance mechanistic insights.

Our provisional response below will be integrated in similar form into the Discussion.

Olivocochlear efferent activity is a potential modulator of OHC gain (by medial olivocochlear neurons, MOC) and afferent activity (by lateral olivocochlear neurons, LOC). Beyond this general observation it is, however, difficult to speculate about its specific role in the TFS1 test, as almost nothing is known about efferent activity under naturalistic conditions in a behaving animal (reviewed by Lauer et al., 2022). We note, however, that efferent activity is believed to be reduced under general anesthesia (reviewed by Guinan, 2011, DOI 10.1007/978-1-4419-7070-1_3) and possibly abnormal in other ways, considering the potential top-down inputs to the efferent neurons from extensive brain networks (reviewed by Schofield, 2011, DOI 10.1007/978-1-4419-7070-1_9; Romero and Trussell, 2022, DOI: 10.1016/j.heares.2022.108516). Thus, it is reasonable to assume a reduced efferent influence in our auditory-nerve data, compared to the behavioral test situation. In contrast, we assume more comparable efferent influences in young-adult and old gerbils. It was recently shown that, despite age-related losses in both MOC and LOC cochlear innervation, this basically reflected the loss of efferent target structures (OHC and type-I afferents), with the surviving cochlear circuitry remaining largely normal (Steenken et al., 2024, DOI: 10.3389/fnsyn.2024.1422330). The main difference was an increased proportion of OHC without any efferent innervation, predominantly in low-frequency cochlear regions (Steenken et al., 2024). Such OHC are thus not under efferent control, and they are more numerous (about 10 – 30%) in old gerbils.

Lastly, although synapse counts did not differ between the low-dose treatment and NH I sham groups, separating these groups rather than combining them with the sham might reveal differences in behavior or AN results, particularly regarding the significance of differences between aged/treatment groups and the young normal-hearing group. For maximizing statistical power, we combined those groups in the statistical analysis. These two groups did not differ in synapse number and had quite similar ABR wave 1 growth functions.

Reviewer #2 (Public review):

Summary:

Using a gerbil model, the authors tested the hypothesis that loss of synapses between sensory hair cells and auditory nerve fibers (which may occur due to noise exposure or aging) affects behavioral discrimination of the rapid temporal fluctuations of sounds. In contrast to previous suggestions in the literature, their results do not support this hypothesis; young animals treated with a compound that reduces the number of synapses did not show impaired discrimination compared to controls. Additionally, their results from older animals showing impaired discrimination suggest that age-related changes aside from synaptopathy are responsible for the age-related decline in discrimination.

We agree with the reviewer’s summary.

Strengths:

(1) The rationale and hypothesis are well-motivated and clearly presented.

(2) The study was well conducted with strong methodology for the most part, and good experimental control. The combination of physiological and behavioral techniques is powerful and informative. Reducing synapse counts fairly directly using ouabain is a cleaner design than using noise exposure or age (as in other studies), since these latter modifiers have additional effects on auditory function.

(3) The study may have a considerable impact on the field. The findings could have important implications for our understanding of cochlear synaptopathy, one of the most highly researched and potentially impactful developments in hearing science in the past fifteen years.

Weaknesses:

(1) My main concern is that the stimuli may not have been appropriate for assessing neural temporal coding behaviorally. Human studies using the same task employed a filter center frequency that was (at least) 11 times the fundamental frequency (Marmel et al., 2015; Moore and Sek, 2009). Moore and Sek wrote: "the default (recommended) value of the centre frequency is 11F0." Here, the center frequency was only 4 or 8 times the fundamental frequency (4F0 or 8F0). Hence, relative to harmonic frequency, the harmonic spacing was considerably greater in the present study. By my calculations, the masking noise used in the present study was also considerably lower in level relative to the harmonic complex than that used in the human studies. These factors may have allowed the animals to perform the task using cues based on the pattern of activity across the neural array (excitation pattern cues), rather than cues related to temporal neural coding. The authors show that mean neural driven rate did not change with frequency shift, but I don't understand the relevance of this. It is the change in response of individual fibers with characteristic frequencies near the lowest audible harmonic that is important here.

The auditory filter bandwidth of the gerbil is about double that of human subjects. Because of this, the masking noise has a larger overall level than in the human studies in the filter. This precludes that the gerbils can use excitation patterns, especially in the condition with a center frequency of 1600 Hz and a fundamental of 200 Hz and in the condition with a center frequency of 3200 Hz and a fundamental of 400 Hz.

The case against excitation pattern cues needs to be better made in the Discussion. It could be that gerbil frequency selectivity is broad enough for this not to be an issue, but more detail needs to be provided to make this argument. The authors should consider what is the lowest audible harmonic in each case for their stimuli, given the level of each harmonic and the level of the pink noise. Even for the 8F0 center frequency, the lowest audible harmonic may be as low as the 4th (possibly even the 3rd). In human, harmonics are thought to be resolvable by the cochlea up to at least the 8th.

Because of the gerbil’s broader auditory filters, with the exception of the condition with center frequency of 1600 Hz and fundamental of 400 Hz harmonics are are not resolved. We will expand the topic of potential excitation pattern cues in the discussion of the revised version and add results on modeled excitation patterns to the supplement.

(2) The synapse reductions in the high ouabain and old groups were relatively small (mean of 19 synapses per hair cell compared to 23 in the young untreated group). In contrast, in some mouse models of the effects of noise exposure or age, a 50% reduction in synapses is observed, and in the human temporal bone study of Wu et al. (2021, https://doi.org/10.1523/JNEUROSCI.3238-20.2021) the age-related reduction in auditory nerve fibres was ~50% or greater for the highest age group across cochlear location. It could be simply that the synapse loss in the present study was too small to produce significant behavioral effects. Hence, although the authors provide evidence that in the gerbil model the age-related behavioral effects are not due to synaptopathy, this may not translate to other species (including human). This should be discussed in the manuscript.

Our provisional response below will be integrated in similar form into the Discussion.

The observed extent of age-related or noise-induced loss of type-I afferent synapses on IHC varies widely between species and studies. For example, in ageing CBA/CaJ mice, mean losses of between 20 and 50% of afferent synapses (depending on cochlear location and precise age) were reported (Sergeyenko et al., 2013, DOI: 10.1523/JNEUROSCI.1783-13.2013; Kobrina et al., 2020, DOI: 10.1016/j.neurobiolaging.2020.08.012). Humans showed more pronounced losses of peripheral axons, of 40–100%, again depending on cochlear location, precise age, and noise history (Wu et al., 2019, DOI: 10.1016/j.neuroscience.2018.07.053; 2021, DOI: 10.1523/JNEUROSCI.3238-20.2021). The age-related and induced synapse losses in our gerbils were in a more moderate range, around 20% (Steenken et al., 2021, DOI: 10.1016/j.neurobiolaging.2021.08.019; this study). Thus, it is possible that a more severe, induced synaptopathy would have resulted in behavioral deficits in young-adult gerbils. However, in the absence of additional noise or pharmacologically induced damage, our study provides strong evidence for other factors causing temporal processing problems with advancing age. Our 3-year-old gerbils are approximately comparable to a 60-year-old human (Castano-Gonzalez et al., 2024, DOI: 10.1016/j.heares.2024.108989) with beginning but not yet clinically relevant hearing loss (Hamann et al., 2002, DOI: 10.1016/S0378-5955(02)00454-9).

It would be informative to provide synapse counts separately for the animals who were tested behaviorally, to confirm that the pattern of loss across the group was the same as for the larger sample.

Yes, the pattern was the same for the subgroup of behaviorally tested animals. We will add this information to the revised version of the manuscript.

(3) The study was not pre-registered, and there was no a priori power calculation, so there is less confidence in replicability than could have been the case. Only three old animals were used in the behavioral study, which raises concerns about the reliability of comparisons involving this group.

The results for the three old subjects differed significantly from those of young subjects and young ouabain-treated subjects. This indicates a sufficient statistical power, since otherwise no significant differences would be observed.

Reviewer #3 (Public review):

This study is a part of the ongoing series of rigorous work from this group exploring neural coding deficits in the auditory nerve, and dissociating the effects of cochlear synaptopathy from other age-related deficits. They have previously shown no evidence of phase-locking deficits in the remaining auditory nerve fibers in quiet-aged gerbils. Here, they study the effects of aging on the perception and neural coding of temporal fine structure cues in the same Mongolian gerbil model.

They measure TFS coding in the auditory nerve using the TFS1 task which uses a combination of harmonic and tone-shifted inharmonic tones which differ primarily in their TFS cues (and not the envelope). They then follow this up with a behavioral paradigm using the TFS1 task in these gerbils. They test young normal hearing gerbils, aged gerbils, and young gerbils with cochlear synaptopathy induced using the neurotoxin ouabain to mimic synapse losses seen with age. In the behavioral paradigm, they find that aging is associated with decreased performance compared to the young gerbils, whereas young gerbils with similar levels of synapse loss do not show these deficits. When looking at the auditory nerve responses, they find no differences in neural coding of TFS cues across any of the groups.

However, aged gerbils show an increase in the representation of periodicity envelope cues (around f0) compared to young gerbils or those with induced synapse loss. The authors hence conclude that synapse loss by itself doesn't seem to be important for distinguishing TFS cues, and rather the behavioral deficits with age are likely having to do with the misrepresented envelope cues instead.

We agree with the reviewer’s summary.

The manuscript is well written, and the data presented are robust. Some of the points below will need to be considered while interpreting the results of the study, in its current form. These considerations are addressable if deemed necessary, with some additional analysis in future versions of the manuscript.

Spontaneous rates - Figure S2 shows no differences in median spontaneous rates across groups. But taking the median glosses over some of the nuances there. Ouabain (in the Bourien study) famously affects low spont rates first, and at a higher degree than median or high spont rates. It seems to be the case (qualitatively) in Figure S2 as well, with almost no units in the low spont region in the ouabain group, compared to the other groups. Looking at distributions within each spont rate category and comparing differences across the groups might reveal some of the underlying causes for these changes. Given that overall, the study reports that low-SR fibers had a higher ENV/TFS log-z-ratio, the distribution of these fibers across groups may reveal specific effects of TFS coding by group.

As the reviewer points out, our sample from the group treated with a high concentration of ouabain showed very few low-spontaneous-rate auditory-nerve fibers, as expected from previous work. However, this was also true, e.g., for our sample from sham-operated animals, and may thus well reflect a sampling bias. We are therefore reluctant to attach much significance to these data distributions. We will consider moving some supplementary information back into the main manuscript when revising.

Threshold shifts - It is unclear from the current version if the older gerbils have changes in hearing thresholds, and whether those changes may be affecting behavioral thresholds. The behavioral stimuli appear to have been presented at a fixed sound level for both young and aged gerbils, similar to the single unit recordings. Hence, age-related differences in behavior may have been due to changes in relative sensation level. Approaches such as using hearing thresholds as covariates in the analysis will help explore if older gerbils still show behavioral deficits.

Unfortunately, we did not obtain behavioral thresholds that could be used here. The ABR thresholds, although not directly comparable to behavioral thresholds, suggest that our old animals had at most a moderate threshold increase in quiet. Furthermore, we want to point out that the TFS 1 stimuli had an overall level of 68 dB SPL, and the pink noise masker would have increased the threshold more than expected from the moderate, age-related hearing loss in quiet. Thus, the masked thresholds for all gerbil groups are likely similar and should have no effect on the behavioral results.

Task learning in aged gerbils - It is unclear if the aged gerbils really learn the task well in two of the three TFS1 test conditions. The d' of 1 which is usually used as the criterion for learning was not reached in even the easiest condition for aged gerbils in all but one condition for the aged gerbils (Fig. 5H) and in that condition, there doesn't seem to be any age-related deficits in behavioral performance (Fig. 6B). Hence dissociating the inability to learn the task from the inability to perceive TFS 1 cues in those animals becomes challenging.

Even in the group of gerbils with the lowest sensitivity, for the condition 400/1600 the animals achieved a d’ of on average above 1. Furthermore, stimuli were well above threshold and audible, even when no discrimination could be observed. Finally, as explained in the methods, different stimulus conditions were interleaved in each session, providing stimuli that were easy to discriminate together with those being difficult to discriminate. This approach ensures that the gerbils were under stimulus control, meaning properly trained to perform the task. Thus, an inability to discriminate does not indicate a lack of proper training.

Increased representation of periodicity envelope in the AN - the mechanisms for increased representation of periodicity envelope cues is unclear. The authors point to some potential central mechanisms but given that these are recordings from the auditory nerve what central mechanisms these may be is unclear. If the authors are suggesting some form of efferent modulation only at the f0 frequency, no evidence for this is presented. It appears more likely that the enhancement may be due to outer hair cell dysfunction (widened tuning, distorted tonotopy). Given this increased envelope coding, the potential change in sensation level for the behavior (from the comment above), and no change in neural coding of TFS cues across any of the groups, a simpler interpretation may be -TFS coding is not affected in remaining auditory nerve fibers after age-related or ouabain induced synapse loss, but behavioral performance is affected by altered outer hair cell dysfunction with age.

A similar point is made by Reviewer #1. As indicated above, we do have limited data on neural bandwidths and will explore if these are sufficient to address the reviewers’ questions about potential, age-related changes in neural tuning in our sample. Previous work found no substantial OHC losses (Tarnowski et al., 1991, DOI: 10.1016/0378-5955(91)90142-V; Adams and Schulte, 1997, DOI: 10.1016/S0378-5955(96)00184-0; Steenken et al., 2024, DOI: 10.3389/fnsyn.2024.1422330) nor any deterioration in neural frequency tuning (Heeringa et al., 2020, DOI: 10.1523/JNEUROSCI.2784-18.2019), in quiet-aged gerbils of similar age as the ones used here.

Emerging evidence seems to suggest that cochlear synaptopathy and/or TFS encoding abilities might be reflected in listening effort rather than behavioral performance. Measuring some proxy of listening effort in these gerbils (like reaction time) to see if that has changed with synapse loss, especially in the young animals with induced synaptopathy, would make an interesting addition to explore perceptual deficits of TFS coding with synapse loss.

This is an interesting suggestion that we will explore in the revision of the manuscript. Reaction times were recorded for responses that can be used as a proxy for listening effort.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study provides convincing evidence on the infraslow oscillation of DG cells during NREM sleep, and how serotonergic innervation modulates hippocampal activity pattern during sleep and memory.

Strengths and Weaknesses:

The authors used state-of-the-art techniques to carry out these experiments. Given that the functional role of infraslow rhythm still remains to be studied, this study provides convincing evidence of the role of DG cells in regulating infraslow rhythm, sleep microarchitecture, and memory.

I have a few minor comments.

(1) Decreased infraslow rhythm during NREMs in the 5ht1a KO mice is striking. It would be helpful to know whether sleep-wake states, MAs, and transitions to REMs are changed.

We agree with the reviewer that serotonin receptors may be involved in sleep regulation therefore it is important to analyze the effect of their manipulation. We would also like to bring to the attention of the reviewer that in this case we restricted the 5ht1a manipulation to the hippocampus which does not have a known impact on sleep-wake regulation. The analysis of our recorded dataset from these mice confirmed this notion, because we did not see any changes in sleep metrics (see: supplementary figure 6A).

(2) It would be interesting to discuss whether the magnitude in changes of infraslow rhythm strength is correlated with memory performance (Figure 6).

We agree with the reviewer that this could be an interesting point. In our experiments we wanted to minimize the impact of the surgical procedures on the behavior, thus we used separate cohorts to record the photometry and to carry out the behavior experiments, therefore we are unable to correlate behavior and infraslow oscillatory amplitudes in our dataset.

However, a similar experiment was carried out in a recent paper where the authors discovered that the norepinephrine system also displays infraslow oscillatory cycles during NREM sleep (Kjaerby et al 2022). The authors of that paper gradually decreased the magnitude of the NE pulses during NREM by optogenetic manipulation of the locus coeruleus which led to a fragmented sleep phenotype characterized by increased micro arousal occurrence, decreased REM and reduced spindle activity. They also tested the memory performance of the mice in a novel object recognition task and found diminished performance level in the opto group. Serotonin has multiple roles in the brain, many of them show overlap with proposed functions of the noradrenergic system including regulation of plasticity, signaling reward or fearful stimuli. Therefore, we speculate that the modification of serotonin dynamics during sleep will most likely interfere with memory performance.

We inserted this paragraph in the discussion part of our paper.

(3) The authors should cite the Oikonomou Neuron paper that describes slow oscillatory activity of DRN SERT neurons during NREM sleep.

Thank you for the suggestion, we inserted this paper in the manuscript.

(4) The authors should clarify how they define the phasic pattern of the photometry signal.

We have added the details in the Methods.

Reviewer #2 (Public review):

Summary:

The authors investigated DG neuronal activity at the population and single-cell level across sleep/wake periods. They found an infraslow oscillation (0.01-0.03 Hz) in both granule cells (GC) and mossy cells (MC) during NREM sleep.

The important findings are:

(1) The antiparallel temporal dynamics of DG neuron activities and serotonin neuron activities/extracellular serotonin levels during NREM sleep, and

(2) The GC Htr1a-mediated GC infraslow oscillation.

Strengths:

(1) The combination of polysomnography, Ca-fiber photometry, two-photon microscopy, and gene depletion is technically sound. The coincidence of microarousals and dips in DG population activity is convincing. The dip in activity in upregulated cells is responsible for the dip at the population level.

(2) DG GCs express excitatory Htr4 and Htr7 in addition to inhibitory Htr1a, but deletion of Htr1a is sufficient to disrupt DG GC infraslow oscillation, supporting the importance of Htr1a in DG activity during NREM sleep.

Weaknesses:

(1) The current data set and analysis are insufficient to interpret the observation correctly.

a. In Figure 1A, during NREM, the peaks and troughs of GC population activities seem to gradually decrease over time. Please address this point.

Thank you for the suggestion. We have analyzed and compared the magnitude of the oscillatory signals in the first and last minute of the NREM sleep epochs in Dock10-Cre mice and found no significant difference. However, we did observe that the ISO amplitude is smaller in the early stage of the first NREM epochs, defined as those with the prior wakefulness longer than 5 minutes (new supplementary figure 1).

b. In Figure 1F, about 30% of Ca dips coincided with MA (EMG increase) and 60% of Ca dips did not coincide with EMG increase. If this is true, the readers can find 8 Ca dips which are not associated with MAs from Figure 1E. If MAs were clustered, please describe this properly.

We did not find evidence that MAs were clustered in our dataset (see a representative example in supplementary figure 1A). We replaced the example trace with a new one which shows calcium dips with and without MAs. We believe this new trace better represents the data.

c. In Figure 1F, the legend stated the percentage during NREM. If the authors want to include the percentage of wake and REM, please show the traces with Ca dips during wake and REM. This concern applies to all pie charts provided by the authors.

Figure 1F (and all other pie charts) shows the outcome of brain states following a calcium-dip episode. That is, we found that the Ca-dips during NREM were followed by MAs in 30% of the cases, 59% of the Ca-dips led to the maintenance of NREM (no MAs) while in 2% and 9% of the cases we detected either REM state or wakening of the animal. These numbers correspond very well with similar analysis done in a recent paper which looked at the infraslow oscillatory behavior of the norepinephrine system (Kjaerby et al 2022) during NREM sleep. We apologize if the wording in the manuscript was misleading, we modified the figure legends to clarify what the pie charts represent. 

d. In Figure 1C, please provide line plots connecting the same session. This request applies to all related figures.

We have replaced the dot plots in all related figures with the line plots. 

e. In Figure 2C, the significant increase during REM and the same level during NREM are not convincing. In Figure 2A, the several EMG increasing bouts do not appear to be MA, but rather wakefulness, because the duration of the EMG increase is greater than 15 seconds. Therefore, it is possible that the wake bouts were mixed with NREM bouts, leading to the decrease of Ca activity during NREM. In fact, In Figure 2E, the 4th MA bout seems to be the wake bout because the EMG increase lasts more than 15 seconds.

We have replaced the Figure 2C with line plots as suggested above. It is clear that MC activity during REM sleep is higher, compared to that in NREM sleep, whereas the overall difference between wake and NREM is not significant (some increased, some decreased). Regarding the MAs, we have added a trace of averaged EMG signals in Figure 2G, showing that the averaged EMG bursts during MA are shorter than 5 seconds.

f. Figure 5D REM data are interesting because the DRN activity is stably silenced during REM. The varied correlation means the varied DG activity during REM. The authors need to address it.

We thank the reviewer for this suggestion. We have added this point to the discussion. We speculate that inputs from the supramammillary nucleus or entorhinal cortex to the DG during REM sleep may both contribute to this variability.

g. In Figure 6, the authors should show the impact of DG Htr1a knockdown on sleep/wake structure including the frequency of MAs. I agree with the impact of Htr1a on DG ISO, but possible changes in sleep bout may induce the DG ISO disturbance.

As suggested, we have performed sleep analysis in the Htr1a knockdown experiments including MA quantification. We have found no significant difference between Hrt1-knockdown and control mice in any of the sleep metrics (see: supplemental figure 6). Our interpretation is that the lack of changes in sleep/wake cycles is likely due to the hippocampus not being directly involved in regulating these brain states.

(2) It is acceptable that DG Htr1a KO induces the reduced freezing in the CFC test (Figure 6E, F), but it is too much of a stretch that the disruption of DG ISO causes impaired fear memory. There should be a correlation.

We have modified the discussion accordingly.

(3) It is necessary to describe the extent of AAV-Cre infection. The authors injected AAV into the dorsal DG (AP -1.9 mm), but the histology shows the ventral DG (Supplementary Figure 4), which reduces the reliability of this study.

The histology image shown in the manuscript was taken from the -2.5 mm anteroposterior level, which we still consider to be part of the dorsal DG. For additional clarity, we have replaced the figure with new histology images slightly more anterior position (AP~2.0mm). 

Reviewer #3 (Public review):

Summary:

The authors employ a series of well-conceived and well-executed experiments involving photometric imaging of the dentate gyrus and raphe nucleus, as well as cell-type specific genetic manipulations of serotonergic receptors that together serve to directly implicate serotonergic regulation of dentate gyrus (DG) granule (GC) and mossy cell (MC) activity in association with an infra slow oscillation (ISO) of neural activity has been previously linked to general cortical regulation during NREM sleep and microarousals.

Strengths:

There are a number of novel and important results, including the modulation of dentage granule cell activity by the infraslow oscillation during NREM sleep, the selective association of different subpopulations of granule cells to microarousals (MA), the anticorrelation of raphe activity with infraslow dentate activity.

The discussion includes a general survey of ISOs and recent work relating to their expression in other brain areas and other potential neuromodulatory system involvement, as well as possible connections with infraslow oscillations, micro-arousals, and sensory sensitivity.

Weaknesses:

(1) The behavioral results showing contextual memory impairment resulting from 5-HT1a knockdown are fine but are over-interpreted. The term memory consolidation is used several times, as well as references to sleep-dependence. This is not what was tested. The receptor was knocked down, and then 2 weeks later animals were found to have fear conditioning deficits. They can certainly describe this result as indicating a connection between 5-HT1a receptor function and memory performance, but the connection to sleep and consolidation would just be speculation. The fact that 5-HT1a knockdown also impacted DG ISOs does not establish dependency. Some examples of this are:

a. The final conclusion asserts "Together, our study highlights the role of neuromodulation in organizing neuronal activity during sleep and sleep-dependent brain functions, such as memory.". However, the reported memory effects (impairment of fear conditioning) were not shown to be explicitly sleep-dependent.

We thank the reviewer for this comment. We have revised the sentence.

b. Earlier in the discussion it mentions "Finally, we showed that local genetic ablation of 5-HT1a receptors in GCs impaired the ISO and memory consolidation". The effect shown was on general memory performance - consolidation was not specifically implicated.

We have revised the sentence.

(2) The assertion on page 9 that the results demonstrate "that the 5-HT is directly acting in the DG to gate the oscillations" is a bit strong given the magnitude of effect shown in Figure 6D, and the absence of demonstration of negative effect on cortical areas that also show ISO activity and could impact DG activity (see requested cortical sigma power analysis).

We have revised the sentence.

(3) Recent work has shown that abnormal DG GC activity can result from the use of the specific Ca indicator being used (GCaMP6s). (Teng, S., Wang, W., Wen, J.J.J. et al. Expression of GCaMP6s in the dentate gyrus induces tonic-clonic seizures. Sci Rep 14, 8104 (2024). https://doi.org/10.1038/s41598-024-58819-9). The authors of that study found that the effect seemed to be specific to GCaMP6s and that GCaMP6f did not lead to abnormal excitability. Note this is of particular concern given similar infraslow variation of cortical excitability in epilepsy (cf Vanhatalo et al. PNAS 2004). While I don't think that the experiments need to be repeated with a different indicator to address this concern, you should be able to use the 2p GCaMP7 experiments that have already been done to provide additional validation by repeating the analyses done for the GCaMP6s photometry experiments. This should be done anyway to allow appropriate comparison of the 2p and photometry results.

We would like to thank the reviewer for this comment. We also analyzed the two-photon data in the same manner as the photometry data. However, the only supportive evidence that might be related to ISO in the two-photon data, recorded at the somatic level, was decreased fluorescence during MAs in the NREM-upregulated cell group (see Figure 3 D, E). We are unsure why this discrepancy exists, but we have discussed it in the manuscript and offered some alternative explanations. One hypothesis we are currently exploring relates to the different subcellular compartments sampled by the two imaging techniques. The photometry probe was implanted above the dentate gyrus, and since light collection efficiency declines sharply with distance from the probe tip (Pisano et al., 2019), we hypothesize that ISO is stronger at the dendritic level which directly receive the inputs from entorhinal cortex, and which is closest to the probe's tip. We are now conducting multiplane two-photon imaging experiments in our labs to test this hypothesis.

(4) While the discussion mentions previous work that has linked ISOs during sleep with regulation of cortical oscillations in the sigma band, oddly no such analysis is performed in the current work even though it is presumably available and would be highly relevant to the interpretation of a number of primary results including the relationship between the ISOs and MAs observed in the DG and similar results reported in other areas, as well as the selective impact of DG 5-HT1a knockdown on DG ISOs. For example, in the initial results describing the cross-correlation of calcium activity and EMG/EEG with MA episodes (paragraph 1, page 4), similar results relating brief arousals to the infraslow fluctuation in sleep spindles (sigma band) have been reported also at .02 Hz associated with variation in sensory arousability (cf. Cardis et al., "Cortico-autonomic local arousals and heightened somatosensory arousability during NREMS of mice in neuropathic pain", eLife 2021). It would be important to know whether the current results show similar cortical sigma band correlations. Also, in the results on ISO attenuation following 5-HT1 knockdown on page 7 (Figure 6), how is cortical EEG affected? Is ISO still seen in EEG but attenuated in DG?

Thank you for this valuable comment. We performed the analysis and found a positive correlation between cortical sigma band activity and DG activity during NREM sleep (see supplementary figure 1C-1E). Additionally, we conducted further analyses using the local 5-HT1a KO mouse model but did not observe significant changes in sleep architecture or MA frequency (see supplementary figure 6A). It is also important to note that ISO was only analyzed using calcium signals, not EEG signals. The standard filtering settings in our EEG data collection (0.5-500 Hz) do not allow us to analyze signals in such a low-frequency range.

(5) The illustrations of the effect of 5-HT1a knockdown shown in Figure 6 are somewhat misleading. The examples in panels B and C show an effect that is much more dramatic than the overall effect shown in panel D. Panels B and C do not appear to be representative examples. Which of the sample points in panel D are illustrated in panels B and C? It is not appropriate to arbitrarily select two points from different animals for comparison, or worse, to take points from the extremes of the distributions. If the intent is to illustrate what the effect shown in D looks like in the raw data, then you need to select examples that reflect the means shown in panel D. It is also important to show the effect on cortical EEG, particularly in sigma band to see if the effects are restricted to the DG ISOs. It would also be helpful to show that MAs and their correlations as shown in Figure 1 or G as well as broader sleep architecture are not affected.

We agree with the reviewer that the chosen example may appear somewhat exaggerated. However, we must point out that visually assessing missing or downregulated frequency components can be challenging. To provide a more objective presentation, we included Supplementary Figure 6B-C, in which we performed analysis similar to that in Fig1G in 5HT1a mice. These figures show a significant decrease in ISO amplitude, though the blockade is not complete, due to the incomplete nature of genetic manipulation with viral injection (see Suppl Fig 5). Furthermore, recent studies (Dong et al., 2023; Zhang et al., 2024; Kjaerby et al., 2022) have identified several other neuromodulatory and peptidergic systems that might affect DG activity during MAs.

To explore this further, we conducted pharmacological experiments. We administered 8-hydroxy-DPAT, a 5-HT1a agonist (i.p. 1 mg/kg) in Dock10-Cre mice injected with AAV-FLEX-GcaMP6s in the DG. Since 5-HT1a receptors act as autoreceptors on raphe 5-HT neurons, this treatment effectively silences the serotonergic system, thereby “removing” 5-HT signaling from the brain. The results, shown in Author response image 1, indicate that pharmacological suppression of 5-HT dampens the ISO in the DG during subsequent sleep intervals, with ISO recovering after the drug is washed out. These findings are consistent with the results obtained with the more specific local genetic manipulation. We have not included this result in the manuscript because we believe that the local downregulation is a cleaner experiment whose interpretation is more straightforward.

Author response image 1.

Finally, we also performed sleep analysis in 5-HT1a KO mice, showing that the local downregulation of 5-HT1a receptors had no significant effect on sleep metrics (Suppl Fig 6A). The hippocampus is not typically involved in regulating sleep-wake cycles, so we believe this result is consistent with that understanding.

(6) On page 9 of the results it states that GCs and MCs are upregulated during NREM and their activity is abruptly terminated by MAs through a 5-HT mediated mechanism. I didn't see anything showing the 5-HT dependence of the MA activity correlation. The results indicate a reduction in ISO modulation of GC activity but not the MA-correlated activity. I would like to see the equivalent of Figure 1,2 G panels with the 5-HT1a manipulation.

We agree with the reviewer on this point. We did not conduct any pharmacological or genetic manipulation in 2-photon calcium imaging experiments. We have removed that statement. As for the suggested analysis, please see our explanation above (Suppl Fig 6B-C).

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Since the authors did not monitor DG neuronal activity with an electrophysiological tool, please rephrase the following sentence: "In this study, we investigated the neuronal activity of the dentate gyrus (DG) with electrophysiological and optical imaging tools during sleep-wake cycles." in the Abstract.

We have rephrased the sentence as suggested.

(2) Since the authors did not manipulate the serotonin release during sleep to investigate whether serotonin release modulates DG ISO, please edit the following sentence: "Further experiments revealed that the infraslow oscillation in the DG is modulated by rhythmic serotonin release during sleep" in the Abstract.

We have rephrased the sentence as suggested.

(3) Single-cell recording in DG with two-photon microscopy may address the issue raised in the 4th paragraph of the Discussion. In addition, in Fig 6C, the photometry has only captured the diminished oscillation in Htr1a KO, but cannot distinguish whether the activity levels of GC remain at high or low, which is a clear disadvantage of photometry.

We agree with the reviewer, and have added text to the discussion.

Reviewer #3 (Recommendations for the authors):

(1) Some of the figures are missing labels in the spectrogram panels (e.g. no freq units in Figures 4 and 6).

We have added information in those figures.

(2) Missing specific locations for EEG electrodes/screws. The text states "we predrilled 2 holes on the right side of the skull (1.5 mm posterior of the Bregma) for implanting recording electrodes". 2 holes on the right side of the skull are pretty vague.

We have added this information in the Methods.

(3) Some additional work that could be cited particularly when discussing the serotonergic impact on hippocampal function as it might relate to sleep and memory would include work linking mesopontine activity (both serotonergic and non-serotonergic) to memory-associated hippocampal sharp-wave ripple activity (e.g. Jelitai et al. Front. Neural Circ. 2021, Wang et al Nat. Neuro. 2015).

We have cited these papers.

(4) The work cited at the beginning of the Results describing higher population calcium activity during sleep states (15,18,30) is generally appropriate but not explicitly related to GCamP imaging. Pilz et al. "Functional Imaging of Dentate Granule Cells in the Adult Mouse Hippocampus", J.Neurosci. 2016 might be a more relevant citation.

We have added the citation.

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

Reviewer #1

Evidence, reproducibility and clarity

Summary: The manuscript by Yang et al. describes a new CME accessory protein. CCDC32 has been previously suggested to interact with AP2 and in the present work the authors confirm this interaction and show that it is a bona fide CME regulator. In agreement with its interaction with AP2, CCDC32 recruitment to CCPs mirrors the accumulation of clathrin. Knockdown of CCDC32 reduces the amount of productive CCPs, suggestive of a stabilisation role in early clathrin assemblies. Immunoprecipitation experiments mapped the interaction of CCDC42 to the α-appendage of the AP2 complex α-subunit. Finally, the authors show that the CCDC32 nonsense mutations found in patients with cardio-facial-neuro-developmental syndrome disrupt the interaction of this protein to the AP2 complex. The manuscript is well written and the conclusions regarding the role of CCDC32 in CME are supported by good quality data. As detailed below, a few improvements/clarifications are needed to reinforce some of the conclusions, especially the ones regarding CFNDS.

Response: We thank the referee for their positive comments. In light of a recently published paper describing CCDC32 as a co-chaperone required for AP2 assembly (Wan et al., PNAS, 2024, see reviewer 2), we have added several additional experiments to address all concerns and consequently gained further insight into CCDC32-AP2 interactions and the important dual role of CCDC32 in regulating CME.

Major comments:

1) Why did the protein could just be visualized at CCPs after knockdown of the endogenous protein? This is highly unusual, especially on stable cell lines. Could this be that the tag is interfering with the expressed protein function rendering it incapable of outcompeting the endogenous? Does this points to a regulated recruitment?

Response: The reviewer is correct, this would be unusual; however, it is not the case. We misspoke in the text (although the figure legend was correct) these experiments were performed without siRNA knockdown and we can indeed detect eGFP-CCDC32 being recruited to CCPs in the presence of endogenous protein. Nonetheless, we repeated the experiment to be certain.

2) The disease mutation used in the paper does not correspond to the truncation found in patients. The authors use an 1-54 truncation, but the patients described in Harel et al. have frame shifts at the positions 19 (Thr19Tyrfs*12) and 64 (Glu64Glyfs*12), while the patient described in Abdalla et al. have the deletion of two introns, leading to a frameshift around amino acid 90. Moreover, to be precisely test the function of these disease mutations, one would need to add the extra amino acids generated by the frame shift. For example, as denoted in the mutation description in Harel et al., the frameshift at position 19 changes the Threonine 19 to a Tyrosine and ads a run of 12 extra amino acids (Thr19Tyrfs*12).

Response: The label of the disease mutant p.(Thr19Tyrfs∗12) and p.(Glu64Glyfs∗12) is based on a 194aa polypeptide version of CCDC32 initiated at a nonconventional start site that contains a 9 aa peptide (VRGSCLRFQ) upstream of the N-terminus we show. Thus, we are indeed using the appropriate mutation site (see: https://www.uniprot.org/uniprotkb/Q9BV29/entry). The reviewer is correct that we have not included the extra 12 aa in our construct; however as these residues are not present in the other CFNDS mutants, we think it unlikely that they contribute to the disease phenotype. Rather, as neither of the clinically observed mutations contain the 78-98 aa sequence required for AP2 binding and CME function, we are confident that this defect contributed to the disease. Thus, we are including the data on the CCDC32(1-54) mutant, as we believe these results provide a valuable physiological context to our studies.

3) The frameshift caused by the CFNDS mutations (especially the one studied) will likely lead to nonsense mediated RNA decay (NMD). The frameshift is well within the rules where NMD generally kicks in. Therefore, I am unsure about the functional insights of expressing a disease-related protein which is likely not present in patients.

Response: We thank the reviewer for bringing up this concern. However, as shown in new Figure S1, the mutant protein is expressed at comparable levels as the WT, suggesting that NMD is not occurring.

4) Coiled coils generally form stable dimers. The typically hydrophobic core of these structures is not suitable for transient interactions. This complicates the interpretation of the results regarding the role of this region as the place where the interaction to AP2 occurs. If the coiled coil holds a stable CCDC32 dimer, disrupting this dimer could reduce the affinity to AP2 (by reduced avidity) to the actual binding site. A construct with an orthogonal dimeriser or a pulldown of the delta78-98 protein with of the GST AP2a-AD could be a good way to sort this issue.

Response: We were unable to model a stable dimer (or other oligomer) of this protein with high confidence using Alphafold 3.0. Moreover, we were unable to detect endogenous CCDC32 co-immunoprecipitating with eGFP-CCDC32 (Fig. S6C). Thus, we believe that the moniker, based solely on the alpha-helical content of the protein is a misnomer. We have explained this in the main text.

Minor comments:

1) The authors interchangeably use the term "flat CCPs" and "flat clathrin lattices". While these are indeed related, flat clathrin lattices have been also used to refer to "clathrin plaques". To avoid confusion, I suggest sticking to the term "flat CCPs" to refer to the CCPs which are in their early stages of maturation.

Response: Agreed. Thank you for the suggestion. We have renamed these structures flat clathrin assemblies, as they do not acquire the curvature needed to classify them as pits, and do not grow to the size that would classify then as plaques.

Significance

General assessment: CME drives the internalisation of hundreds of receptors and surface proteins in practically all tissues, making it an essential process for various physiological processes. This versatility comes at the cost of a large number of molecular players and regulators. To understand this complexity, unravelling all the components of this process is vital. The manuscript by Yang et al. gives an important contribution to this effort as it describes a new CME regulator, CCDC32, which acts directly at the main CME adaptor AP2. The link to disease is interesting, but the authors need to refine their experiments. The requirement for endogenous knockdown for recruitment of the tagged CCDC32 is unusual and requires further exploration.

Advance: The increased frequency of abortive events presented by CCDC32 knockdown cells is very interesting, as it hints to an active mechanism that regulates the stabilisation and growth of clathrin coated pits. The exact way clathrin coated pits are stabilised is still an open question in the field.

Audience: This is a basic research manuscript. However, given the essential role of CME in physiology and the growing number of CME players involved in disease, this manuscript can reach broader audiences.

Response: We thank the referee for recognizing the 'interesting' advances our studies have made and for considering these studies as 'an important contribution' to 'an essential process for various physiological processes' and able 'to reach broader audiences'. We have addressed and reconciled the reviewer's concerns in our revised manuscript.

Field of expertise of the reviewer: Clathrin mediated endocytosis, cell biology, microscopy, biochemistry.

Reviewer #2

Evidence, reproducibility and clarity

In this manuscript, the authors demonstrate that CCDC32 regulates clathrin-mediated endocytosis (CME). Some of the findings are consistent with a recent report by Wan et al. (2024 PNAS), such as the observation that CCDC32 depletion reduces transferrin uptake and diminishes the formation of clathrin-coated pits. The primary function of CCDC32 is to regulate AP2 assembly, and its depletion leads to AP2 degradation. However, this study did not examine AP2 expression levels. CCDC32 may bind to the appendage domain of AP2 alpha, but it also binds to the core domain of AP2 alpha. Overall, while this work presents some interesting ideas, it remains unclear whether CCDC32 regulates AP2 beyond the assembly step.

Response: We thank the reviewer for drawing our attention to the Wan et al. paper, that appeared while this work was under review. However, our in vivo data are not fully consistent with the report from Wan et al. The discrepancies reveal a dual function of CCDC32 in CME that was masked by complete knockout vs siRNA knockdown of the protein, and also likely affected by the position of the GFP-tag (C- vs N-terminal) on this small protein. Thus:

• Contrary to Wan et al., we do not detect any loss of AP2 expression (see new Figure S3A-B) upon siRNA knockdown. Most likely the ~40% residual CCDC32 present after siRNA knockdown is sufficient to fulfill its catalytic chaperone function but not its structural role in regulating CME beyond the AP2 assembly step.
• Contrary to Wan et al., we have shown that CCDC32 indeed interacts with intact AP2 complex (Figure S3C and 6B,C) showing that all 4 subunits of the AP2 complex co-IP with full length eGFP-CCDC32. Interestingly, whereas the full length CCDC32 pulls down the intact AP2 complex, co-IP of the ∆78-98 mutant retains its ability to pull down the b2-µ2 hemicomplex, its interactions with α:σ2 are severely reduced. While this result is consistent with the report of Wan et al that CCDC32 binds to the α:σ2 hemi-complex, it also suggests that the interactions between CCDC32 and AP2 are more complex and will require further studies.

• Contrary to Wan et al., we provide strong evidence that CCDC32 is recruited to CCPs. Interestingly, modeling with AlphaFold 3.0 identifies a highly probably interaction between alpha helices encoded by residues 66-91 on CCDC32 and residues 418-438 on a. The latter are masked by µ2-C in the closed confirmation of the AP2 core, but exposed in the open confirmation triggered by cargo binding, suggesting that CCDC32 might only bind to membrane-bound AP2. Thus, our findings are indeed novel and indicate striking multifunctional roles for CCDC32 in CME, making the protein well worth further study.

• Besides its role in AP2 assembly, CCDC32 may potentially have another function on the membrane. However, there is no direct evidence showing that CCDC32 associates with the plasma membrane.

Response: We disagree, our data clearly shows that CCDC32 is recruited to CCPs (Fig. 1B) and that CCPs that fail to recruit CCDC32 are short-lived and likely abortive (Fig. 1C). Wan et al. did not observe any colocalization of C-terminally tagged CCDC32 to CCPs, whereas we detect recruitment of our N-terminally tagged construct, which we also show is functional (Fig. 6F). Further, we have demonstrated the importance of the C-terminal region of CCDC32 in membrane association (see new Fig. S7). Thus, we speculate that a C-terminally tagged CCDC32 might not be fully functional. Indeed, SIM images of the C-terminally-tagged CCDC32 in Wan et al., show large (~100 nm) structures in the cytosol, which may reflect aggregation.

CCDC32 binds to multiple regions on AP2, including the core domain. It is important to distinguish the functional roles of these different binding sites.

Response: We have localized the AP2-ear binding region to residues 78-99 and shown these to be critical for the functions we have identified. As described above we now include data that are complementary to those of Wan et al. However, our data also clearly points to additional binding modalities. We agree that it will be important and map these additional interactions and identify their functional roles, but this is beyond the scope of this paper.

AP2 expression levels should be examined in CCDC32 depleted cells. If AP2 is gone, it is not surprising that clathrin-coated pits are defective.

Response: Agreed and we have confirmed this by western blotting (Figure S3A-B) and detect no reduction in levels of any of the AP2 subunits in CCDC32 siRNA knockdown cells. As stated above this could be due to residual CCDC32 present in the siRNA KD vs the CRISPR-mediated gene KO.

If the authors aim to establish a secondary function for CCDC32, they need to thoroughly discuss the known chaperone function of CCDC32 and consider whether and how CCDC32 regulates a downstream step in CME.

Response: Agreed. We have described the Wan et al paper, which came out while our manuscript was in review, in our Introduction. As described above, there are areas of agreement and of discrepancies, which are thoroughly documented and discussed throughout the revised manuscript.

The quality of Figure 1A is very low, making it difficult to assess the localization and quantify the data.

Response: The low signal:noise in Fig. 1A the reviewer is concerned about is due to a diffuse distribution of CCDC32 on the inner surface of the plasma membrane. We now, more explicitly describe this binding, which we believe reflects a specific interaction mediated by the C-terminus of CCDC32; thus the degree of diffuse membrane binding we observe follows: eGFP-CCDC32(FL)> eGFP-CCDC32(∆78-98)>eGFP-CCDC32(1-54)~eGFP/background (see new Fig. S7). Importantly, the colocalization of CCDC32 at CCPs is confirmed by the dynamic imaging of CCPs (Fig 1B).

In Figure 6, why aren't AP2 mu and sigma subunits shown?

Response: Agreed. Not being aware of CCDC32's possible dual role as a chaperone, we had assumed that the AP2 complex was intact. We have now added this data in Figure 6 B,C and Fig. S3C, as discussed above.

Page 5, top, this sentence is confusing: "their surface area (~17 x 10 nm2) remains significantly less than that required for the average 100 nm diameter CCV (~3.2 x 103 nm2)."

Response: Thank you for the criticism. We have clarified the sentence and corrected a typo, which would definitely be confusing. The section now reads, "While the flat CCSs we detected in CCDC32 knockdown cells were significantly larger than in control cells (Fig. 4D, mean diameter of 147 nm vs. 127 nm, respectively), they are much smaller than typical long-lived flat clathrin lattices (d{greater than or equal to}300 nm)(Grove et al., 2014). Indeed, the surface area of the flat CCSs that accumulate in CCDC32 KD cells (mean ~1.69 x 104 nm2) remains significantly less than the surface area of an average 100 nm diameter CCV (~3.14 x 104 nm2). Thus, we refer to these structures as 'flat clathrin assemblies' because they are neither curved 'pits' nor large 'lattices'. Rather, the flat clathrin assemblies represent early, likely defective, intermediates in CCP formation."

Significance

Please see above.(from above: Overall, while this work presents some interesting ideas, it remains unclear whether CCDC32 regulates AP2 beyond the assembly step)

Response: Our responses above argue that we have indeed established that CCDC32 regulates AP2 beyond the assembly step. We have also identified several discrepancies between our findings and those reported by Wan et al., most notably binding between CCDC32 and mature AP2 complexes and the AP2-dependent recruitment of CCDC32 to CCPs. It is possible that these discrepancies may be due to the position of the GFP tag (ours is N-terminal, theirs is C-terminal; we show that the N-terminal tagged CCDC32 rescues the knockdown phenotype, while Wan et al., do not provide evidence for functionality of the C-terminal construct).

__Reviewer #3 __

Evidence, reproducibility and clarity (Required):

In this manuscript, Yang et al. characterize the endocytic accessory protein CCDC32, which has implications in cardio-facio-neuro-developmental syndrome (CFNDS). The authors clearly demonstrate that the protein CCDC32 has a role in the early stages of endocytosis, mainly through the interaction with the major endocytic adaptor protein AP2, and they identify regions taking part in this recognition. Through live cell fluorescence imaging and electron microscopy of endocytic pits, the authors characterize the lifetimes of endocytic sites, the formation rate of endocytic sites and pits and the invagination depth, in addition to transferrin receptor (TfnR) uptake experiments. Binding between CCDC32 and CCDC32 mutants to the AP2 alpha appendage domain is assessed by pull down experiments. Together, these experiments allow deriving a phenotype of CCDC32 knock-down and CCDC32 mutants within endocytosis, which is a very robust system, in which defects are not so easily detected. A mutation of CCDC32, known to play a role in CFNDS, is also addressed in this study and shown to have endocytic defects.

Response: We thank the reviewer for their positive remarks regarding the quality of our data and the strength of our conclusions.

In summary, the authors present a strong combination of techniques, assessing the impact of CCDC32 in clathrin mediated endocytosis and its binding to AP2, whereby the following major and minor points remain to be addressed:

• The authors show that CCDC32 depletion leads to the formation of brighter and static clathrin coated structures (Figure 2), but that these were only prevalent to 7.8% and masked the 'normal' dynamic CCPs. At the same time, the authors show that the absence of CCDC32 induces pits with shorter life times (Figure 1 and Figure 2), the 'majority' of the pits. Clarification is needed as to how the authors arrive at these conclusions and these numbers. The authors should also provide (and visualize) the corresponding statistics. The same statement is made again later on in the manuscript, where the authors explain their electron microscopy data. Was the number derived from there?

These points are critical to understanding CCDC32's role in endocytosis and is key to understanding the model presented in Figure 8. The numbers of how many pits accumulate in flat lattices versus normal endocytosis progression and the actual time scales could be included in this model and would make the figure much stronger.

Response: Thank you for these comments. We understand the paradox between the visual impression and the reality of our dynamic measurements. We have been visually misled by this in previous work (Chen et al., 2020), which emphasizes the importance of unbiased image analysis afforded to us through the well-documented cmeAnalysis pipeline, developed by us (Aguet et al., 2013) and now used by many others (e.g. (He et al., 2020)).

The % of static structures was not derived from electron microscopy data, but quantified using cmeAnalysis, which automatedly provides the lifetime distribution of CCPs. We have now clarified this in the manuscript and added a histogram (Fig. S4) quantifying the fraction of CCPs in lifetime cohorts 150s (static).

• In relation to the above point, the statistics of Figure 2E-G and the analysis leading there should also be explained in more detail: For example, what are the individual points in the plot (also in Figures 6G and 7G)? The authors should also use a few phrases to explain software they use, for example DASC, in the main text.

Response: Each point in these bar graphs represents a movie, where n{greater than or equal to}12. These details have been added to the respective figure legend. We have also added a brief description of DASC analysis in the text.

• There are several questions related to the knock-down experiments that need to be addressed:

Firstly, knock-down of CCDC32 does not seem to be very strong (Figure S2B). Can the level of knock-down be quantified?

Response: We have now quantified the KD efficiency. It is ~60%. This turns out to be fortuitous (see responses to reviewer 2), as a recent publication, which came out after we completed our study, has shown by CRISPR-mediated knockout, that CCD32 also plays an essential chaperone function required for AP2 assembly. We do not see any reduction in AP2 levels or its complex formation under our conditions (see new Supplemental Figure S3), which suggests that the effects of CCDC32 on CCP dynamics are more sensitive to CCDC32 concentration than its roles as a chaperone. Our phenotypes would have been masked by more efficient depletion of CCDC32.

In page 6 it is indicated that the eGFP-CCDC32(1-54) and eGFP-CCDC32(∆78-98) constructs are siRNA-resistant. However in Fig S2B, these proteins do not show any signal in the western blot, so it is not clear if they are expressed or simply not detected by the antibody. The presence of these proteins after silencing endogenous CCDC32 needs to be confirmed to support Figures 6 and Figures 7, which critically rely on the presence of the CCDC32 mutants.

Response: Unfortunately, the C-terminally truncated CCDC32 proteins are not detected because they lack the antibody epitope, indeed even the D78-98 deletion is poorly detected (compare the GFP blot in new S1A with the anti-CCDC32 blot in S1B). However, these constructs contain the same siRNA-resistance mutation as the full length protein. That they are expressed and siRNA resistant can be seen in Fig. S2A (now Fig. S1A) blotting for GFP.

In Figures 6 and 7, siRNA knock-down of CCDC32 is only indicated for sub-figures F to G. Is this really the case? If not, the authors should clarify. The siRNA knock-down in Figure 1 is also only mentioned in the text, not in the figure legend. The authors should pay attention to make their figure legends easy to understand and unambiguous.

Response: No, it is not the case. Thank you for pointing out the uncertainty. We have added these details to the Figure legends and checked all Figure legends to ensure that they clearly describe the data shown.

• It is not exactly clear how the curves in Figure 3C (lower panel) on the invagination depth were obtained. Can the authors clarify this a bit more? For example, what are kT and kE in Figure 3A? What is I0? And how did the authors derive the logarithmic function used to quantify the invagination depth? In the main text, the authors say that the traces were 'logarithmically transformed'. This is not a technical term. The authors should refer to the actual equation used in the figure.

Response: This analysis was developed by the Kirchhausen lab (Saffarian and Kirchhausen, 2008). We have added these details and reference them in the Figure legend and in the text. We also now use the more accurate descriptor 'log-transformed'.

• In the discussion, the claim 'The resulting dysregulation of AP2 inhibits CME, which further results in the development of CFNDS.' is maybe a bit too strong of a statement. Firstly, because the authors show themselves that CME is perturbed, but by no means inhibited. Secondly, the molecular link to CFNDS remains unclear. Even though CCDC32 mutants seem to be responsible for CFNDS and one of the mutant has been shown in this study to have a defect in endocytosis and AP2 binding, a direct link between CCDC32's function in endocytosis and CFNDS remains elusive. The authors should thus provide a more balanced discussion on this topic.

Response: We have modified and softened our conclusions, which now read that the phenotypes we see likely "contribute to" rather than "cause" the disease.

• In Figure S1, the authors annotate the presence of a coiled-coil domain, which they also use later on in the manuscript to generate mutations. Could the authors specify (and cite) where and how this coiled-coil domain has been identified? Is this predicted helix indeed a coiled-coil domain, or just a helix, as indicated by the authors in the discussion?

Response: See response to Reviewer 1, point 4. We have changed this wording to alpha-helix. The 'coiled-coil' reference is historical and unlikely a true reflection of CCDC32 structure. AlphaFold 3.0 predictions were unable to identify with certainly any coiled-coil structures, even if we modelled potential dimers or trimers; and we find no evidence of dimerization of CCDC32 in vivo. We have clarified this in the text.

Minor comments

• In general, a more detailed explanation of the microscopy techniques used and the information they report would be beneficial to provide access to the article also to non-expert readers in the field. This concerns particularly the analysis methods used, for example: How were the cohort-averaged fluorescence intensity and lifetime traces obtained? How do the tools cmeAnalysis and DASC work? A brief explanation would be helpful.

Response: We have expanded Methods to add these details, and also described them in the main text.

• The axis label of Figure 2B is not quite clear. What does 'TfnR uptake % of surface bound' mean? Maybe the authors could explain this in more detail in the figure legend? Is the drop in uptake efficiency also accessible by visual inspection of the images? It would be interesting to see that.

Response: This is a standard measure of CME efficiency. 'TfnR uptake % of surface bound' = Internalized TfnR/Surface bound TfnR. Again, images may be misleading as defects in CME lead to increased levels of TfnR on the cell surface, which in turn would result in more Tfn uptake even if the rate of CME is decreased.

• Figure 4: How is the occupancy of CCPs in the plasma membrane measured? What are the criteria used to divide CCSs into Flat, Dome or Sphere categories?

Response: We have expanded Methods to add these details. Based on the degree of invagination, the shapes of CCSs were classified as either: flat CCSs with no obvious invagination; dome-shaped CCSs that had a hemispherical or less invaginated shape with visible edges of the clathrin lattice; and spherical CCSs that had a round shape with the invisible edges of clathrin lattice in 2D projection images. In most cases, the shapes were obvious in 2D PREM images. In uncertain cases, the degree of CCS invagination was determined using images tilted at {plus minus}10-20 degrees. The area of CCSs were measured using ImageJ and used for the calculation of the CCS occupancy on the plasma membrane.

• Figure 5B: Can the authors explain, where exactly the GFP was engineered into AP2 alpha? This construct does not seem to be explained in the methods section.

Response: We have added this information. The construct, which corresponds to an insertion of GFP into the flexible hinge region of AP2, at aa649, was first described by (Mino et al., 2020) and shown to be fully functional. This information has been added to the Methods section.

• Figure S1B: The authors should indicate the colour code used for the structural model.

Response: We have expanded our structural modeling using AlphaFold 3.0 in light of the recent publication suggesting the CCDC32 interacts with the µ2 subunit and does not bind full length AP2. These results are described in the text. The color coding now reflects certainty values given by AlphaFold 3.0 (Fig. S6B, D).

• The list of primers referred to in the materials and methods section does not exist. There is a Table S1, but this contains different data. The actual Table S1 is not referenced in the main text. This should be done.

Response: We apologize for this error. We have now added this information in Table S2.

__ Significance (Required):__

In this study, the authors analyse a so-far poorly understood endocytic accessory protein, CCDC32, and its implication for endocytosis. The experimental tool set used, allowing to quantify CCP dynamics and invagination is clearly a strength of the article that allows assessing the impact of an accessory protein towards the endocytic uptake mechanism, which is normally very robust towards mutations. Only through this detailed analysis of endocytosis progression could the authors detect clear differences in the presence and absence of CCDC32 and its mutants. If the above points are successfully addressed, the study will provide very interesting and highly relevant work allowing a better understanding of the early phases in CME with implication for disease.

The study is thus of potential interest to an audience interested in CME, in disease and its molecular reasons, as well as for readers interested in intrinsically disordered proteins to a certain extent, claiming thus a relatively broad audience. The presented results may initiate further studies of the so-far poorly understood and less well known accessory protein CCDC32.

Response: We thank the reviewer for their positive comments on the significance of our findings and the importance of our detailed phenotypic analysis made possible by quantitative live cell microscopy. We also believe that our new structural modeling of CCDC32 and our findings of complex and extensive interactions with AP2 make the reviewers point regarding intrinsically disordered proteins even more interesting and relevant to a broad audience. We trust that our revisions indeed address the reviewer's concerns.

The field of expertise of the reviewer is structural biology, biochemistry and clathrin mediated endocytosis. Expertise in cell biology is rather superficial.

References:

Aguet, F., Costin N. Antonescu, M. Mettlen, Sandra L. Schmid, and G. Danuser. 2013. Advances in Analysis of Low Signal-to-Noise Images Link Dynamin and AP2 to the Functions of an Endocytic Checkpoint. Developmental Cell. 26:279-291.

Chen, Z., R.E. Mino, M. Mettlen, P. Michaely, M. Bhave, D.K. Reed, and S.L. Schmid. 2020. Wbox2: A clathrin terminal domain-derived peptide inhibitor of clathrin-mediated endocytosis. Journal of Cell Biology. 219.

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Reviewer #3 (Public review):

In this paper, the authors use a three-phase economic game to examine the tendency to engage in prosocial versus competitive exchanges with three anonymous partners. In particular, they consider individual differences in the tendency to infer about others' tendencies based on one's preferences and to update one's preferences based on observations of others' behavior. The study includes a sample of individuals diagnosed with borderline personality disorder and a matched sample of psychiatrically healthy control participants.

On the whole, the experimental design is well-suited to the questions and the computational model analyses are thorough, including modern model-fitting procedures. I particularly appreciated the clear exposition regarding model parameterization and the descriptive Table 2 for qualitative model comparison. My broad question about the experiment (in terms of its clinical and cognitive process relevance): Does the task encourage competition or give participants a reason to take advantage of others? I don't think it does, so it would be useful to clarify the normative account for prosociality in the introduction (e.g., some of Robin Dunbar's work).

The finding that individuals with BPD do not engage in self-other generalization on this task of social intentions is novel and potentially clinically relevant. The authors find that BPD participants' tendency to be prosocial when splitting points with a partner does not transfer into their expectations of how a partner will treat them in a task where they are the passive recipient of points chosen by the partner. In the discussion, the authors reasonably focus on model differences between groups (Bayesian model comparison), yet I thought this finding -- BPD participants not assuming prosocial tendencies in phase 2 while CON participant did -- merited greater attention. Although the BPD group was close to 0 on the \beta prior in Phase 2, their difference from CON is still in the direction of being more mistrustful (or at least not assuming prosociality). This may line up with broader clinical literature on mistrustfulness and attributions of malevolence in the BPD literature (e.g., a 1992 paper by Nigg et al. in Journal of Abnormal Psychology). My broad point is to consider further the Phase 2 findings in terms of the clinical interpretation of the shift in \beta relative to controls.

On the conceptual level, I had two additional concerns. First, the authors note that they have "proposed a theory with testable predictions" (p. 4 but also elsewhere) but they do not state any clear predictions in the introduction, nor do they consider what sort of patterns will be observed in the BPD group in view of extant clinical and computational literature. Rather, the paper seems to be somewhat exploratory, largely looking at group differences (BPD vs. CON) on all of the shared computational parameters and additional indices such as belief updating and reaction times. Given this, I would suggest that the authors make stronger connections between extant research on intention representation in BPD and their framework (model and paradigm). In particular, the authors do not address related findings from Ereira (2020) and Story (2024) finding that in a false belief task that BPD participants *overgeneralize* from self to other. A critical comparison of this work to the present study, including an examination of the two tasks differ in the processes they measure, is important.

In addition, perhaps it is fairer to note more explicitly the exploratory nature of this work. Although the analyses are thorough, many of them are not argued for a priori (e.g., rate of belief updating in Figure 2C) and the reader amasses many individual findings that need to by synthesized.

Second, in the discussion, the authors are too quick to generalize to broad clinical phenomena in BPD that are not directly connected to the task at hand. For example, on p. 22: "Those with a diagnosis of BPD also show reduced permeability in generalising from other to self. While prior research has predominantly focused on how those with BPD use information to form impressions, it has not typically examined whether these impressions affect the self." Here, it's not self-representation per se (typically, identity or one's view of oneself), but instead cooperation and prosocial tendencies in an economic context. It is important to clarify what clinical phenomena may be closely related to the task and which are more distal and perhaps should not be approached here.

On a more technical level, I had two primary concerns. First, although the authors consider alternative models within a hierarchical Bayesian framework, some challenges arise when one analyzes parameter estimates fit separately to two groups, particularly when the best-fitting model is not shared. In particular, although the authors conduct a model confusion analysis, they do not as far I could tell (and apologies if I missed it) demonstrate that the dynamics of one model are nested within the other. Given that M4 has free parameters governing the expectations on the absolute and relative reward preferences in Phase 2, is it necessarily the case that the shared parameters between M1 and M4 can be interpreted on the same scale? Relatedly, group-specific model fitting has virtues when believes there to be two distinct populations, but there is also a risk of overfitting potentially irrelevant sample characteristics when parameters are fit group by group.

To resolve these issues, I saw one straightforward solution (though in modeling, my experience is that what seems straightforward on first glance may not be so upon further investigation). M1 assumes that participants' own preferences (posterior central tendency) in Phase 1 directly transfer to priors in Phase 2, but presumably the degree of transfer could vary somewhat without meriting an entirely new model (i.e., the authors currently place this question in terms of model selection, not within-model parameter variation). I would suggest that the authors consider a model parameterization fit to the full dataset (both groups) that contains free parameters capturing the *deviations* in the priors relative to the preceding phase's posterior. That is, the free parameters $\bar{\alpha}_{par}^m$ and $\bar{\beta}_{par}^m$ govern the central tendency of the Phase 2 prior parameter distributions directly, but could be reparametrized as deviations from Phase 1 $\theta^m_{ppt}$ parameters in an additive form. This allows for a single model to be fit all participants that encompasses the dynamics of interest such that between-group parameter comparisons are not biased by the strong assumptions imposed by M1 (that phase 1 preferences and phase 2 observations directly transfer to priors). In the case of controls, we would expect these deviation parameters to be centred on 0 insofar as the current M1 fit them best, whereas for BPD participants should have significant deviations from earlier-phase posteriors (e.g., the shift in \beta toward prior neutrality in phase 2 compared to one's own prosociality in phase 1). I think it's still valid for the authors to argue for stronger model constraints for Bayesian model comparison, as they do now, but inferences regarding parameter estimates should ideally be based on a model that can encompass the full dynamics of the entire sample, with simpler dynamics (like posterior -> prior transfer) being captured by near-zero parameter estimates.

My second concern pertains to the psychometric individual difference analyses. These were not clearly justified in the introduction, though I agree that they could offer potentially meaningful insight into which scales may be most related to model parameters of interest. So, perhaps these should be earmarked as exploratory and/or more clearly argued for. Crucially, however, these analyses appear to have been conducted on the full sample without considering the group structure. Indeed, many of the scales on which there are sizable group differences are also those that show correlations with psychometric scales. So, in essence, it is unclear whether most of these analyses are simply recapitulating the between-group tests reported earlier in the paper or offer additional insights. I think it's hard to have one's cake and eat it, too, in this regard and would suggest the authors review Preacher et al. 2005, Psychological Methods for additional detail. One solution might be to always include group as a binary covariate in the symptom dimension-parameter analyses, essentially partialing the correlations for group status. I remain skeptical regarding whether there is additional signal in these analyses, but such controls could convince the reader. Nevertheless, without such adjustments, I would caution against any transdiagnostic interpretations such as this one in the Highlights: "Higher reported childhood trauma, paranoia, and poorer trait mentalizing all diminish other-to-self information transfer irrespective of diagnosis." Since many of these analyses relate to scales on which the groups differ, the transdiagnostic relevance remains to be demonstrated.

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Reply to the reviewers

*We are grateful for the overall positive feedback and constructive suggestions. We have been able to experimentally address several of the suggested points and provide here a revision plan addressing all of the reviewers’ additional concerns. *

*In summary, this study is of fundamental novelty and high impact as it: *

1. Reveals an unexpected role of ErbB3 in controlling ____Integrin β1 ____trafficking ____and thus epithelial cell motility and extracellular vesicles secretion. This may shed important insights into the role of ErbB3____ in cancer.
2. Uncovers the first ligand-independent, non-canonical cellular function for ErbB3 as a scaffold for the Arf6-Rabaptin5-GGA3 endosomal sorting complex.
3. Provoking the notion that pseudo-RTKs may have evolved cellular functions beyond receptor signaling, such as by scaffolding endosomal sorting compartments. *We hope that you share our view that these conceptually ground breaking findings will be of interest to a broad cross-disciplinary audience interested in cell signaling, cancer biology, endocytic trafficking and integrin biology. *

1. Point-by-point description of the revisions

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

ErbB3 is well-known for its significance in cancer, which is dependent on ligand-binding and heterodimerization with other ErbB family members. In the current work, Rodrigues-Junior et al. identified novel, unexpected functions of ErbB3 in promoting early endocytic recycling and restricting exocytic trafficking (extracellular vesicles secretion) of membrane receptors, such as integrin b1 and transferrin receptor, via stabilizing the Arf6-GGA3-Rabaptin5 endosomal sorting complex. Via ErbB3 siRNA knockdown, they observed an impaired recycling of transferrin receptor and integrin b1 back to the cell membrane. The recycling assay condition (growth factor-deprived) provided a very clean result to support that this ErbB3-dependent endocytic trafficking is ligand-binding independent. The trafficking-dependence on ErbB3 (both the endocytic and the exocytic) was further supported by integrin b1 functional assays (scratch closure assay and Matrigel invasion assay). There are still some details that need to be clarified to fully understand the conclusion.

Major points:

1. • The manuscript started with a pathological correlation between high ErbB3 level and poor patient survival rate. In Fig.1, the impaired TfR recycling, and the co-localization between ErbB3 and integrin b1 were also performed in the pathological breast cancer cell line, MCF7. While investigating integrin b1 recycling, the authors suddenly switched to another two non-malignant human breast epithelial cell lines, which led to a difficult correlation of ErbB3-mediated recycling back to the disease situation. The authors should state more clearly this point, rather than data not shown. This inconsistency occurred also in other assays, for example, when addressing the trafficking from TGN to cell surface, MCF7 was utilized; while when addressing extracellular vesicle secretion, MCF10A was utilized. Response: we thank the reviewer for the comment. The rationale for using different cell-lines or primary cells is now better explained in the manuscript. We found that depletion of ErbB3 impaired recycling of Integrin β1 in the non-malignant cells, including MCF10A and primary breast epithelial cells, but not in malignant MCF7 cells that overexpress ErbB3 (data not shown). We now speculate in the manuscript that perhaps the dependence on ErbB3 for Integrin b1 recycling is lost at some point during carcinogenesis, although further studies will be needed to address this possibility. MCF7 cells were used to detect endogenous ErbB3 as normal expression levels of ErbB3 (primary MECs and MCF10A) were not detectable by immunofluorescence microscopy in our hands with a range of antibodies we tested. With regard to the transferrin recycling assay, we first attempted to use MCF10A cells for consistency, however we found that transferrin internalized poorly in these cells and the limited pool of transferrin that internalised was retained in these cells for an extended time (3 h), thus rendering them unsuitable for our transferrin experiments. *

*Concerning the data on trafficking from the TGN to cell surface we mistakenly wrote that they were performed in MCF7 cells although they were in fact done in MCF10A cells. This is now corrected in the new version of this manuscript. *

Additionally, based on the constructive comment by this reviewer, we have now extended the analysis of EV secretion in ErbB3, Rab4 and Rabaptin5 silenced cells to MCF7 cells. The new data is in line with our findings in MCF10A and prHMEC cells, that absence of ErbB3 significantly increased EV secretion. Moreover, Rab4 and Rabaptin5 knockdown also enhanced the amount of EVs secreted by MCF7 cells. These results were incorporated in the manuscript as new Supplementary Figure S7F-G and new Supplementary Figure S9F-G, as recommended. Furthermore, we also included in this new version that GGA3 and to a lesser extent Rab GTPase-binding effector protein 1 (Rabaptin5 or RABPT5) shared colocalisation with endogenous ErbB3 in MCF7 cells as the new Supplementary Figure 9A, B. Finally, we also attempted to conduct the Arf6 IP in MCF7 cells, but as opposed to MCF10A cells, the yield of Arf6 in pull down experiments was much lower than in MCF10A cells, and interacting proteins were not detectable.

It was shown before that ErbB3 undergoes constitutive internalization and degradation within several hours that is independent of ligand-binding (ref#13). Can the authors provide experimental evidences to show the correlation of TfR or integrin b1 recycling with this dynamic ErbB3 levels rather than ErbB3 knockdown?

Response: we have performed colocalization of ErbB3, traced Integrin β1 and the recycling endosome marker EHD1, showing triple colocalization in a subset of endosomes, as shown in the new Supplementary Figure S2H. Experimental limitations prevented us from including EEA1 in triple staining for mCherry-ErbB3 or endogenous ErbB3 protein. Furthermore, ectopically expressed ErbB3 in MCF10A cells did not show convincing co-localisation. We hope that the new EHD1 triple colocalization with ErbB3 and Integrin β1 in endosomal compartments satisfies this specific comment.

As mentioned above, regarding the transferrin recycling assay, we first attempted to use MCF10A cells for consistency, however we found that transferrin internalized poorly in these cells and the limited pool of transferrin that internalised was retained in these cells for an extended time (3 h), thus preventing their use.

The efficiency of siRNA knockdown of ErbB3 (both #1 and #2) should support the observed phenotype (Fig. 1I-J, K-L). Is there a correlation between the ErbB3 level with integrin recycling? For example, siRNA#2 led to more efficient knockdown of ErbB3 in MCF10A?

Response: notably, the immunoblots presented here to assess the efficiency of the two different siRNAs are one example and we noted some variability between different experiments but find that both siRNAs work well and yield comparable effects on recycling of Integrin β1. Importantly, the recycling data represents biological repeats of independently performed experiments, and have yielded reproducible and consistent ErbB3 silencing using both siRNAs. This is noted by the lack of significance between ErbB3 knocked down cells in Fig. 1I-J and K-L. Hence, we consider that both siRNAs against ErbB3 worked efficiently with comparable outcome. Please also note our reply to Rev2 #07.

ErbB3 loss led to more extracellular vesicles secretion, but also lysosomal degradation of integrin b1. This conclusion is supported by results shown in Fig.4D-E and Fig. S8A-B, while the analysis from the same cell line (MCF10A, Fig. S3A) results in no change of integrin b1 levels upon ErbB3 depletion. Fig. S3B showed also no change in a second non-malignant cell line (prHMEC). How do the authors explain this conflict?

Response*: we thank the reviewer for this comment. We believe that the increase in EV secretion and lysosomal degradation is compensated by increase in de novo synthesis of Integrin β1 (see data below, from Fig. S3C). In the original manuscript we did not perform the appropriate statistical analysis of the RT-qPCR data. The unpaired two-tail Student’s T-test is only suitable for normally distributed samples, which is not the case here. Instead, we performed the appropriate Mann-Whitney U-test assuming non-normal distribution, yielding an exact p-value of 0.017. The figure S3A and associated text has been modified accordingly. *

Minor points: 1. Is TfR also colocalizing with endogenous ErbB3?

*Response: as mentioned in the major comment #02, we attempted to perform the transferrin recycling assay using MCF10A cells to enable direct comparisons with the integrin b1 recycling, but found that transferrin internalized poorly in these cells. *

Fig. 3J, TSG101, T is masked by 3I

Response: we apologize for this oversight. We have gone through the manuscript in detail and corrected all pointed errors accordingly.

Page 10, the description of the EV secretion in prHMEC cells is annotated to the wrong figure. Fig S5Dà S7D; S5Eà S7E

Response: we apologize for this oversight and have now corrected the mistake.

Fig. 4M: How was the motility/invasion into Matrigel determined? Images? Only quantifications are shown.

Response*: the matrigel invasion assay was described in the Material and Methods section. Accordingly, the data were expressed as the percentage of invasion based on the ratio of the mean number of cells invading through Matrigel matrix per mean number of cells in the uncoated support. For this rebuttal letter, the reviewer can find representative images of invaded MCF10A siCtrl non-treated (Ctrl) or treated with VSF secreted from MCF10A siCtrl or siErbB3. Since this is an established method to measure cell invasion, we hope the reviewer agrees that these images do not add value to the manuscript. *

Fig. 4M: Exosomes collected from ErbB3-depleted cells promotes the migration in MCF10A-wild type cells, how about the effects on ErbB3-depleted cells? This group should be included for analysis.

Response*: as proposed, we have treated both control and ErbB3-silenced MCF10A cells with normalized concentrations of EVs secreted from siCtrl and siErbB3 (1 x 109 nanoparticles/ mL) for 48 hours, followed by cell viability and cell invasion assays. The new data show that both EV pools modestly increased cell viability and substantially increased invasiveness of both wild-type and ErbB3-depleted cells through Matrigel (new Figures 4K and L). Together, our results indicate that while ErbB3-silenced MCF10A cells exhibited lower basal motility, ErbB3 is not required for the observed EV induced motility. The new Figures 4K and L were included and further discussed in this manuscript. *

Quantification of the blots should be provided for Fig. 5A (GGA3), 5B (GGA3, Rabaptin5 and Arf6), 5F (GGA3) and 5G (GGA3, Rabaptin5 and Arf6). What is mock IP in each graph? The mock IP is neither mentioned in methods nor in legends.

Response*: we have now carried out densitometry analysis in all the requested immunoblots shown in Figure 5. We also changed the mock IP term to IgG IP for clarity. The use of non-immunogenic IgG in control IPs is now specified in the methods and respective figure legend. *

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

Summary: In their manuscript, Rodrigues-Junior and colleagues identify a novel ligand-independent function of the tyrosine kinase receptor (RTK) ErbB3 as a regulator of integrin β1 recycling. In particular, the authors demonstrate that ErbB3 depletion reduce β1 integrin surface expression, triggering its lysosomal degradation and increasing its secretion in extracellular vesicles (EVs). Moreover, the authors show that these EVs enhanced the invasive capacity of ErbB3 wild type breast epithelial cells. In addition, the authors evidence the interaction between ErbB3, GGA3 and Rabaptin5. Loss of any of these proteins destabilizes this interaction, which abrogates integrin β1 recycling and leads to its degradation and secretion. The work is potentially interesting; however, there are some aspects that need to be analyzed in a more robust manner.

Major comments:

1. The manuscript is mainly focused on β1 integrin endocytic and post-endocytic fate following ErbB3 silencing, describing also a molecular mechanism underlying these observations. Despite the cited manuscript by Deneka, A. and colleagues indicates a similar mechanism for transferrin receptor (TfR) recycling, the Authors only studied the receptor internalization upon ErbB3 silencing. Therefore, this observation does not add any significance to the main topic of the manuscript and its removal should be considered. Response*: we agree with the reviewer the fate of Integrin β1 is the main focus of this manuscript. We would however favour retaining the TfR data as it implies a wider role of ErbB3, beyond trafficking of Integrin β1. We ask for the reviewer’s understanding of our rationale. *

2.Data from Figure S1A seems to be not normally distributed. Have the Authors tested the data for normal distribution? If not, please consider it. If the data is not normally distributed, a non parametric Mann-Whitney U-Test would be more suitable.

Response: we thank the reviewer for the comment. The differential ErbB3 mRNA expression analysis was retrieved from the widely used GEPIA2 portal (to date about 600 manuscripts cite this portal on PubMed), based on the selected datasets (“TCGA tumors vs TCGA normal + GTEx normal” or “TCGA tumors vs TCGA normal”). The method for differential analysis is one-way ANOVA, using disease state (Tumor or Normal) as variable for calculating differential expression, as it considers differential expression among several tumors.

Tang, Z., Kang, B., Li, C., Chen, T., and Zhang, Z. (2019). GEPIA2: an enhanced web server for large-scale expression profiling and interactive analysis. Nucleic Acids Res. 47, W556–W560. https://doi.org/10.1093/nar/gkz430.

1. The Authors studied the colocalization of ErbB3, Rab4 and Rab11, observing an increased colocalization between ErbB3 and Rab4 10 minutes following primaquine. However, the Authors previously referred to Sönnichsen, B et al. manuscript, in which TfR colocalized with Rab11 at 30min. It would be interesting to see whether ErbB3 and Rab11 colocalize at later time points in the presence or absence of primaquine. This will reinforce the conclusion that ErbB3 is involved in early Rab4-dependent recycling.

Response: we appreciate the reviewer’s comment. However, we consider that these requested experiments will not add significant value to the novelty of this manuscript and hope that the reviewer accepts that we politely refrain from reproducing them.

In Figure 4C the Authors observed a reduction in β1 integrin levels in ErbB3 silenced cells compared to the control already at the beginning of tracing (0 min), which might be due to accelerated turnover at the internalization step of their experimental design. To confirm this, immunofluorescence of β1 integrin in control and ErbB3 silenced cells could be performed just right after the 15min integrin internalization.

Response: this is likely a misunderstanding as the timepoint (0 min) is defined as the point after the 15 min internalization step when the imaging-based tracing begins, which aligns perfectly with the reviewer’s request.

In the discussion, the Authors indicate that "loss of ErbB3 redirects Integrin β1 towards lysosomes for degradation, mimicking loss of GGA3 that similarly redirects both Integrin β1 and c-Met towards lysosomal degradation, or Rabaptin5 depletion that we find similarly redirects trafficking of internalised Integrin β1 towards lysosomal degradation". However, the involvement of lysosomal degradation was only studied for ErbB3 silencing by employing chloroquine. To further support this statement, the use of chloroquine in Rabaptin5- and GGA3-depleted cells is recommended.

Response: we appreciate the reviewer’s comment, but since these findings have been published earlier, we think that they will not add significant value to the manuscript and hope that the reviewer accepts that we politely refrain from reproducing them.

Minor comments:

6.The Authors should consider shortening the following sentences from the Introduction: "GGA proteins contain several functional domains that...thereby regulating sorting of cargo including Integrin β3 and TfR into recycling endosomes".

Response: we thank the reviewer for the comment. We have now divided this sentence into two for smoother reading.

The Authors do not show ErbB3 silencing efficiency at the protein level until Figure 3G, which should have been shown in Figure 1 or Supplementary Figure 1, as all the research is based on it. Moreover, GGA3 silencing efficiency was never tested.

Response*: we thank the reviewer for this comment. We have included a new immunoblot confirming the silencing of ErbB3 by two independent siRNAs in MCF7 cells, as the new Supplementary Figure S2A. Please, note that GGA3 silencing was shown in the main Figure 6J. *

Figure 1I and Figure 1K may include the representative images for the missing siErbB3 to properly illustrate the associated quantification.

Response: we thank the reviewer for the comment. We have now included the representative images, as suggested.

Consider including a Western blot showing the effect of lapatinib in EGFR, ErbB2 and ErbB3 protein expression, including their phosphorylated forms.

Response: we thank the reviewer for the comment. As requested, we now show that at used concentration, lapatinib efficiently blocked tyrosine phosphorylation of ErbB3 and ERK1/2, without perturbing EGFR or ErbB3 expression levels. We also considered it relevant to show that 1 µM lapatinib used was not cytotoxic to MCF10A and MCF7 cells. We hope that these new results satisfy this specific request.

Some supplementary figures are mislabelled, such as Supplementary Figure S5D and S5E on page 10, which should be S7D and S7E, respectively. Supplementary Figure S7C on page 15 should be S9C.

Response: we apologize for this oversight and have performed the corrections.

The following sentence on page 8 should be revised as a verb is missing: "which corresponds to the reported peak time when colocalization of Rab4 with traced TfR, preceding Rab11 and TfR colocalization that peaks later at 30 minutes".

Response: we apologize for this oversight. It now reads: "which corresponds to the reported peak time of colocalization of Rab4 with traced TfR, which precedes Rab11 and TfR colocalization that peaks later at 30 minutes".

The main text indicates that the amount of VSV-G transported to the cell surface after 30min it is not affected by ErbB3 silencing. However, in Figure 3E seems to slightly decrease following the silencing. The Authors may consider employing another Western blot image to match the main text and the quantification in Figure 3F.

Response: as the reviewer noted the immunoblot showed a slight decrease. It is however a very modest decrease that is also observed in the positive control (MUC1) in the same Streptavidin IP sample. We ask for permission to keep these representative images.

In the main text, a significant difference in the nanoparticles/cell between ErbB3-depleted cells and wild type or control cells were reported. However, Figure 3I only showed the statistics of each siRNA vs the control and not the wild type condition.

Response: we apologize for this oversight. We removed from the text the comparison with the wild-type non-transfected cells to avoid misunderstanding.

The Authors concluded that "chloroquine treatment significantly restored traced Integrin β1 levels". However, this conclusion is not reflected in the statistical analysis reported in Figure 4H, which only showed the differences between control and ErbB3 silenced cells. Thus, the statistics reported for the chloroquine results should be added.

Response: we appreciate the comment by the reviewer. The requested comparison is now included in the new Figure 4H.

The Authors concluded that "loss of either GGA3 or Rabaptin5 mimics the effect of loss of ErbB3 on endocytic trafficking of Integrin β1, consistent with the hypothesis that GGA3 and Rabaptin5 are effectors of ErbB3 in promoting endosomal recycling and impeding EV release". To confirm this conclusion, the inclusion of siRabaptin5 results in Figures 6H and 6J is suggested.

Response*: we thank the reviewer for the comment. We have now included immunoblots of MCF10A cell lysate after silencing ErbB3 or Rabaptin5, as the results shown in the previous Figure 6G. We believe that these new data satisfy the specific request. *

To be consistent with the results presentation:

• The inclusion of Modal size is recommended in Figure 6I.

• Some graphs show the number of cells or biological replicates while other ones no.

• Figure 4E showed different time points for both siRNAs.

Response: we appreciate the comment and we have now included as the new main Figure 6H the modal size for the EVs secreted by MCF10A cells upon Rabaptin5 silencing. We will ensure that all respective Figure legends indicate the number of replicates. The intermediate time points showed in the main Figure 4E are different, however since the final read out at 9 h using two independent siRNAs against ErbB3 are directly comparable we ask permission to maintain the time points with respect to the analysis we performed.

Figure 1E represents the squared regions of Figure 1D, but it is not indicated in the figure legend.

Response: we apologize for this oversight. We have now indicated in Figure 1 legend that Figure 1E represents the squared regions of Figure 1D, as suggested.

In the legend of Figure 1D-G, 30min of integrin internalization is reported, where it should be 15min according to main text and methods.

Response: we apologize for this oversight and we thank the reviewer for this comment. We have now indicated the correct time point in Figure 1 legend.

The addition of representative images in Figure 6A is recommended, as already present in Figure 1I.

Response: we thank the reviewer for the comment. Representative images of Fig. 6A-D were included as the new panel Fig. 6B.

As two different siRNAs for ErbB3 were used and not in all experiments, the employed siRNA should be indicated in each experiment. In the cases where both ErbB3 siRNAs were employed, figures should report them either as main results or supplementary.

Response: we appreciate this meticulous comment. We have now indicated in the figure and in the respective figure legends which siRNA was used in the respective set of experiments (siErbB3 #01 or #02).

Why do the Authors use EVs enriched in the VSF or by UC to show the same result? What is the criteria to choose one or the other one? For example, in Figures 6G and 6K.

Response*: based on the guidelines suggested by MISEV 2018 and 2023, there is no gold standard method for EV isolation. Thus, by using at least two independent methods (i.e., tangential flow filtration, followed by immuno-affinity and ultracentrifugation; UC) we validate the enrichment of EVs in our sample preparations, showing reproducible results among the different EV enrichment protocols (Figure 3). *

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

The paper by Dorival Mendes Rodrigues-Junior et al., focuses on a novel ligand-independent role of ErbB3 receptor, modulating Transferrin receptor and integrin beta1 early recycling. Authors perform several in vitro studies where they show how ErbB3 depletion diverts integrin beta1 from recycling towards lysosomal degradation and extracellular vesicle secretion, impairing cell migration. They also provide mechanistic experiments showing the role of ErbB3 on Arf6-GGA3-Rabaptin5 endosomal complex assembly.

Major comments:

1. Fig. 1. Authors should co-stain with early endosomal markers (such as EEA1) to clearly show endogenous ErbB3 and Beta1 integrin endosomal co-localization. Including some insets with higher magnifications would also improve visual inspection of such interactions. Response: as requested, we have performed colocalization of ErbB3, traced Integrin β1 and the recycling endosome marker EHD1, showing triple colocalization in a subset of endosomes, as shown in the new Supplementary Figure S2H. Experimental limitations prevented us from including EEA1 in triple staining for mCherry-ErbB3 or endogenous ErbB3 protein. Furthermore, ectopically expressed ErbB3 in MCF10A cells did not show convincing co-localisation with EEA. We believe that the new triple colocalization showing ErbB3 and Integrin β1 in EHD1-positive endosomal compartments satisfies this specific comment.

Fig. 1H and 1I. Authors need to provide TIRF penetration depth to better evaluate the potential cytosolic contribution. Additionally, plasma membrane purification studies would help to validate their live imaging results.

Response: the TIRF penetration depth was 83nm which has now been added to the methods section. Purifications of plasma membrane fractions, following recycling of traced surface-labelled Integrin β1 in control or siErbB3 depleted cells, by cell surface biotinylation and immunoblotting of the recovered proteins is indeed a valuable approach to validate our findings. Nevertheless, we are confident about the results of our confocal imaging results. Thus, including these results might not contribute significantly to the novelty of this manuscript. Hence, we ask permission to publish the paper at this stage, without the plasma membrane purification, as this requires optimizations and will delay the publication of our paper, in addition to exhausting our limited financial resources.

Fig. 1J. Authors should explain better how they calculated normalized fluorescence.

Response: the normalized fluorescence is explained in the Fig. 1J legend and in the respective method section. Alexa488 intensity was normalized between 0-1, with the control as reference where Fnorm=((Fmax-Fmin)/(F-Fmin)). All data points were background corrected, followed by normalization to the pre-stimulatory level (F/F0).

Fig. 2B. Authors should include some plasma membrane markers (such as WGA) to better localize cell surface after beta1 integrin tracing.

Response: we appreciate the reviewer’s comment, and have attempted the suggested experiment, but in our hands, WGA did not give a clear membrane staining but a diffuse faint signal in MCF10A cells for reasons we do not fully understand.

Fig. 1J, 1M-1L: beta1 integrin endocytic recycling should be compared across the same time-points to better evaluate kinetic differences.

Response: the intermediate time points showed in the main Figure 1J, M-L are based on the final read out. We understand that it could be interesting evaluating the kinetic differences but this will generate a substantial number of comparisons that might be difficult for visualization. We ask permission to keep the comparisons among the latest respective time points with respect to the performed analysis.

Fig. 3. Author should consider adding additional experiments with Rab4 and Rab11 dominant negative forms to validate their results.

Response: the experiments proposed have been performed, but the ectopic expression of dominant negative Rab4 and Rab11 had detrimental effects to the cells, with the formation of large endosomal blobs and rounding up of the MCF10A cells. Subsequently we do not feel confident with the possible conclusions from these data. We ask the reviewer to understand this technical detail and accept the fact that we are not able to address this point.

Fig. 4M. To validate authors' claim on the role of integrin Beta1-containing EVs on invasive behaviour, they should repeat the experiment using blocking beta1 antibodies prior to EV addition.

Response*: we thank the reviewer for this comment. As requested, we performed the experiment using the Integrin β1 blocking monoclonal antibody (mAb; clone P4C10). The new data show that P4C10A treatment alone or in combination with EVs derived from MCF10A cells transfected with siCtrl or siErbB3 significantly reduced invasiveness in comparison to IgG treatments, confirming the mechanistic role of Integrin β1 promoting MCF10A invasive behaviour. The new Figure 4M was included and further discussed in this manuscript. *

While authors claim that their results could potentially clarify different aspects of tumour dissemination, most of their experiments are done in MCF10A, a non-tumorigenic epithelial cell line. To better support their conclusion, they should reproduce key experiments in MCF7 or other tumorigenic cell line.

Response: we thank the reviewer for the comment. As explained in response to reviewer 1, the rational for using different cell-lines or primary cells is now better explained in the manuscript. We found that depletion of ErbB3 impaired recycling of Integrin β1 in the normal non-malignant cells including MCF10A and primary breast epithelial cells, but not in malignant MCF7 cells that overexpress ErbB3 (data not shown), which is now discussed in the paper. Moreover, *MCF7 cells were used to detect endogenous ErbB3 as normal expression levels of ErbB3 (primary MECs and MCF10A) were not detectable by immunofluorescence microscopy with a range of antibodies we tested. Furthermore, we also included in this new version that GGA3 and Rab GTPase-binding effector protein 1 (Rabaptin5 or RABPT5) shared colocalisation with endogenous ErbB3 in MCF7 cells as the new Supplementary Figure 9A, B. Finally, we also attempted to conduct the Arf6 IP in MCF7 cells, but as opposed to MCF10A cells, the yield of Arf6 in pull down experiments was much lower than in MCF10A cells, and interacting proteins were not detectable. *

Minor comments:

1. Fig. 1D-1F: please explain better if beta1 integrin surface signal was quenched in these specific set of studies. Response: Beta1 Integrin was quenched on ice with an antibody against Alexa488 as described by Arjonen et al. (Traffic, 2012; DOI: 10.1111/j.1600-0854.2012.01327.x), and further outlined in the methods section and results section (page 6 and schematic Fig4A).

Suppl. Fig. 3A: last WB lane should read "siErB2" instead of "siErbB3".

Response: we thank the reviewer and we apologize for this oversight. We corrected the siErbB2 lane in Supplementary Figure 3A, as requested.

Author response:

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

eLife Assessment:

This study provides valuable insights, addressing the growing threat of multi-drug-resistant (MDR) pathogens by focusing on the enhanced efficacy of colistin when combined with artesunate and EDTA against colistin-resistant Salmonella strains. The evidence is solid, supported by comprehensive microbiological assays, molecular analyses, and in vivo experiments demonstrating the effectiveness of this synergic combination. However, the discussion on the clinical application challenges of this triple combination is incomplete, and it would benefit from addressing the high risk associated with using three potential nephrotoxic agents in vivo.

The development of novel pharmaceutical dosage forms, pharmacokinetic, pharmacodynamic and safety analysis of the triple combination will be further conducted in our next study to provide a theoretical basis for the next clinical drug use. The discussion of potential toxicity of AS, colistin, EDTA and the triple combination have been added in line 318 to 337.

Public Reviews:

Reviewer #1 (Public Review):

(1) The study focuses on a limited number of Salmonella strains, and broader testing on various MDR pathogens would strengthen the findings.

The number of COL-resistant clinical strains that actually used was larger than that mentioned in our original article, when evaluating the antimicrobial activities of AS, EDTA, COL alone or drug combinations. But, considering that there were superfluous results of mcr-1 positive Salmonella strains, we omitted these results (Table supplement 7 and 8 in revised supplement materials) to avoid redundant data presentation in the original article. Additionally, much more gram-negative and -positive MDR bacteria, such as Klebsiella pneumoniae, Pseudomonas aeruginosa and Staphylococcus aureus will be selected for the next study including the development of novel pharmaceutical dosage forms, pharmacokinetic, pharmacodynamic and safety analysis et al.

(2) While the study elucidates several mechanisms, further molecular details could provide deeper insights into the interactions between these drugs and bacterial targets.

In our next study, further molecular details will be focused on the regulatory targets of CheA and SpvD-related pathways, as well as the precise inhibition targets of MCR protein by the triple combination, through the generation of deletion or point mutations, and analysis of intermolecular interactions.

(3) The time-kill experiment was conducted over 12 hours instead of the recommended 24 hours. To demonstrate a synergistic effect among the drugs, a reduction of at least 2 log10 in colony count should be shown in a 24-hour experiment. Additionally, clarifying the criteria for selecting drug concentrations is important to improve the interpretation of the results.

The time-kill experiment of 24 hours have been re-executed and could be used to replace the Figure 1 in the original paper. The New Figure 1 has been uploaded and the change do not affect our interpretation of the result.

Although in vitro studies have determined that with increasing dose of AS and EDTA, the antibacterial synergistic activity was gradually enhanced, and meanwhie, may also resulting in more toxic side effects. Thus, in our study, the 1/8 MICs of AS and EDTA were selected to ensure excellent antibacterial activity whereas minimize the potential toxicity. The instructions on the selection of drug concentration have been added in line 323 to 326.

(4) While the combination of EDTA, artesunate, and colistin shows promising in vitro results against Salmonella strains, the clinical application of this combination warrants careful consideration due to potential toxicity issues associated with these compounds.

The development of novel pharmaceutical dosage forms, pharmacokinetic, pharmacodynamic and safety analysis of the triple combination will be further conducted in our next study to provide a theoretical basis for the next clinical drug use.

Reviewer #2 (Public Review):

(1) The study by Zhai et al describes repurposing of artesunate, to be used in combination with EDTA to resensitize Salmonella spp. to colistin. The observed effect applied both to strains with and without mobile colistin resistance determinants (MCR). It was already known that EDTA in combination with colistin has an inhibitory effect on MCR-enzymes, but at the same time, both colistin and EDTA can contribute to nephrotoxicity, something which is also true for artesunate. Thus, the triple combination of three nephrotoxic agents has significant challenges in vivo, which is not particularly discussed in this paper.

The discussion of potential toxicity of triple combination has been added in line 318 to 337.

(2) The selection of strains is not very clear. Nothing is known about the sequence types of the strains or how representative they are for strains circulating in general. Thus, it is difficult to generalize from this limited number of isolates, although the studies done in these isolates are comprehensive.

The tested strains in this study were all COL-resistant clinical isolates, and the genome sequencing and comparative analysis of these strains have not been analyzed. The antibacterial activities of different antimicrobial drugs against the S16 and S30 strains have been measured and listed in the Table supplement 9 within revised supplement materials. Considering that the number of COL-resistant clinical strains that actually used was larger than that mentioned in our original article (see the NO.1 response to the Public Reviewer #1), we think that the results obtained in this study could be representative to some extent.

(3) Nothing is known about the susceptibility of the strains to other novel antimicrobial agents. Colistin has a limited role in the treatment of gram-negative infections, and although it can be used sometimes in combination, it is not clear why it would be combined with two other nephrotoxic agents and how this could have relevance in a clinical setting.

The antibacterial activities of different antimicrobial drugs against the S16 and S30 strains have been measured and listed in the Table supplement 9 within revised supplement materials. Additionally, the discussion of potential toxicity of triple combination has been added in line 318 to 337.

(4) It is not clear whether their transcriptomics analysis should at least be carried out in duplicate for reasons of being able to assess reproducibility. It is also not clear why the samples were incubated for 6 hours - no discussion is presented on the selection of a time point for this.

As it can be seen from the time kill curves that the survival number of bacteria started to decrease after 4 h incubation of drug combinations. If the incubation time is too short (for example less than 4 h), the differentially expressed genes can not be fully revealed, while too long incubation time (such as 8 h and 12 h) may lead to a significant CFU reduction of bacteria, and result in inaccurate sequencing results. Therefore, we selected the incubation time 6 h, at which point drugs exhibited  significant antibacterial effects and there were also enough survival bacteria in the sample for transcriptome analysis. Each sample had three replications to preserve the accuracy of results.

(5) Discussion is lacking on the reproducibility and selection of details for the methodology.

The results obtained in this paper have been repeated several times, which indicated that the detailed operation steps described in the materials and methods section were reproducibility. To avoid redundancy, we did not include too much details in the discussion section.

Reviewer #3 (Public Review):

(1) Number of strains tested.

The number of COL-resistant clinical strains that actually used was larger than that mentioned in our original article (see the NO.1 response to the Public Reviewer #1)

(2) Response to comment: Lack of data on cytotoxicity.

The pharmacokinetic, pharmacodynamic and safety analysis of the triple combination will be further conducted in our next study to provide a theoretical basis for the next clinical drug use.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

(1) Introduction:

The introduction should provide more context about the pathogen Salmonella, its significance in both human and veterinary medicine, and the impact of colistin resistance in these pathogens. Salmonella is a leading cause of foodborne illnesses worldwide, resulting in substantial morbidity and mortality. It can cause a range of diseases, from gastroenteritis to more severe systemic infections like typhoid fever and invasive non-typhoidal salmonellosis. In veterinary medicine, Salmonella infections can lead to significant economic losses in livestock industries due to illness and death among animals, as well as through the contamination of animal products.

The description has been added in the introduction section in line 47 to 53.

(2) Results and Discussion:

(1) While the combination of EDTA, artesunate, and colistin shows promising in vitro results against Salmonella, the clinical application of this combination warrants careful consideration due to potential toxicity issues associated with these compounds. Colistin is known for nephrotoxicity and neurotoxicity, limiting its use to severe cases where the benefits outweigh the risks. EDTA, as a chelating agent, can disrupt essential metal ions in the body, posing risks of metabolic imbalances. Although it has clinical applications, primarily in cases of heavy metal poisoning, its use as an adjuvant in antibiotics may present risks. Although generally well-tolerated for malaria, interactions of artesunate with other drugs and long-term safety in combined therapies require thorough investigation.

The discussion of potential toxicity of triple combination has been added in line 318 to 337.

(2) Table 1: The manuscript mentions that some strains used in the study are mcr-positive and mcr-negative. It is important to indicate in Table 1, in addition to the identification of Salmonella species, which strains are mcr-positive or mcr-negative.

The relevant information has been added in Table 1.

(3) Figure 2: What is the authors' hypothesis regarding the growth curves labeled "a" and "e" where strains JS and S16 resume growth 12 hours after treatment with AS? In the legend of Figure 2, describe what was used as the "positive control group."

The growth curves labeled “a” and “e” were in Figure 1. After incubated with AC for 8 h, the survival CFUs of JS and S16 strains showed a slightly reduction, but there were still living cells. Since the bactericidal activity of AC is not strong enough to exert sustained bactericidal activity, these remaining living cells will resume growth after treatment with AC for 12 h. The “positive control group” in the legend of Figure 2 has been indicated in line 724.

(4) What is the authors' hypothesis for the differences observed in the transcriptome and metabolome?

The changes in gene transcription level may cause corresponding changes in protein level, but these proteins are not all involved in the bacterial metabolic process. For example, MCR protein  is encoded by the COL resistance related gene mcr, which mediates the modification of lipid A, but are not involved in the cellular metabolic process. Therefore, the transcriptome change of mcr gene may affect the protein production of MCR, nor the bacterial metabolic processes, so there are differences observed in the transcriptome and metabolome.

(5) In some parts of the text, the authors state that artesunate and EDTA potentiate the action of colistin, which is a bacteriostatic drug. However, in other parts, the authors describe the effect of the AEC combination as bacteriostatic (Abstract: line 32; Results: line 179). How do the authors explain this inconsistency?

The artesunate and EDTA could be regarded as “adjuvants” for the bacteriostatic drug colistin. Adjuvants itself act no or weak antibacterial effect on bacteria. For antimicrobial drugs, the “adjuvants” are compounds that generally used in combination with antibacterial drugs to re-sensitizing bacteria that have developed drug resistance. Thus, in this paper the AEC combination could be regared as bacteriostatic.

(6) According to Brennan & Kirby (2019; doi: 10.1016/j.cll.2019.04.002), to evaluate the synergism between different drug combinations, bacterial growth curves need to be assessed over 24 hours. If the colony count is {greater than or equal to} 2 log10 lower than that of the most active antimicrobial alone, the combination is considered synergistic. Based on the growth curve results shown in Figure 1, the experiment was conducted for 12 hours, and in some cases, only a small reduction in growth was observed, even at the maximum concentration of colistin. Moreover, in some cases, the curve resumes rising between 8 and 12 hours. What is the authors' hypothesis in this case? It is important to conduct the assay over 24 hours to confirm the synergism between these drugs.

The time-kill experiment of 24 hours have been re-executed and could be used to replace the Figure 1 in the original paper. Additionally, the phenomenon that “the curve resumes rising between 8 and 12 hours” has been explained in the response to comment of “Reviewer #1 (Recommendations For The Authors), Results and Discussion, (3) Figure 2”.

(7) To prove that CheA and SpvD play a critical role in the effect of the AEC combination, deletion of these genes should be performed, and the mutant strains should be tested.

The deletion of cheA and spvD will be carried out in our next study.

(8) To demonstrate that the flagellum is no longer assembled, a transmission electron microscopy image using antibodies against flagellin should be performed, along with motility tests.

The motility assays have been performed and displayed as Figure supplement 5 in the revised supplement materials.

(9) Figure 7: In the X-axis legend, specify what "model" refers to.

The “model” refers to the PBS control group that mice were treated with PBS after the intraperitoneal injection of 100 µL bacterial solution (1.31 × 10⁵ CFU).

(10) Figure 8 Legend: In the legend of Figure 8 (line 717), are the authors referring to E. coli or Salmonella?

It referred to Salmonella, which has already been illustrated in the headline of Figure 8 in the revised manuscript.

(3) Materials and Methods:

(1) Bacterial Strains and Agents: It would be beneficial to include in the table the species of the strains used in the study, as well as the concentrations of colistin, artesunate, and EDTA utilized (lines 321 - 332).

We have ever tried to add the above information to Table 1, but the addition of this information would make the table too large and beyond the margins, which is not conducive to the layout design of the table, so we chose to display these information in the materials and methods section instead of the table.

(2) Antibacterial Activity In Vitro: Ensure clarity and well-defined ranges for the concentrations of colistin, EDTA, and artesunate used separately and in combinations (lines 335 - 344).

The drug concentrations have been listed in line 369 to 371.

(3) Time-Kill Assays: Clarify the criteria for selecting concentrations, whether based on MICs or peak and trough concentrations relevant to human and animal treatments with colistin (lines 345 - 351).

Although in vitro studies have determined that with increasing dose of AS and EDTA, the antibacterial synergistic activity was gradually enhanced, and meanwhie, may also resulting in more toxic side effects. Thus, in our study, the 1/8 MICs of AS and EDTA were selected to ensure excellent antibacterial activity whereas minimize the potential toxicity. The instructions on the selection of drug concentration have been added in line 323 to 326.

(4) General Corrections: Throughout the manuscript, correct typographical errors and consistently include the concentration values in mg/L alongside the MIC fractions. Specify the strains used for all experiments to ensure clarity. In the manuscript, the term "medication regimens" is used to describe the experimental setups involving different combinations of drugs tested in vitro. To improve accuracy and clarity, it is recommended to use the term "drug combination" instead. This term is more appropriate for in vitro experiments and will help avoid confusion with clinical treatment protocols.

The typographical errors have been checked and corrected throughout the manuscript, and the “medication regimens” have been replaced by “drug combinations”.

Reviewer #2 (Recommendations For The Authors):

Please see above for recommendations on what can be done to improve the manuscript.

While other omics analyses have been conducted herein, the authors do not comment on the genomic analysis of their own strains. It would have been a natural step to sequence all the strains used in the experiments.

Due to limited program funding, the genome sequencing and comparative analysis of these strains have not been analyzed. The antibacterial activities of different antimicrobial drugs against the S16 and S30 strains have been measured and listed in the Table supplement 9 within revised supplement materials.

Some minor comments:

(1) There are some spelling errors - e.g. "bacteria strains" instead of "bacterial strains".

The grammar and spelling errors have been corrected throughout the manuscript.

(2) I would avoid words like "unfortunately".

The word “unfortunately” has been changed.

(3) Some MIC-values in Table 1 seem incorrect - e.g. 24 mg/L. This is not a 2-log value - the value should be 32 mg/L if the dilution series has been carried out correctly.

We are so sorry for the mistake. The data has been corrected, and we also checked other data.

Reviewer #3 (Recommendations For The Authors):

Below are some suggestions.

(1) Sentences L47 & L48 "Infections with antibiotic-resistant pathogens, especially carbapenemase-producing Enterobacteriaceae, represent an impending catastrophe of a return to the pre-antibiotic era" - this is slightly exaggerated! I also wonder if we need to use Enterobacterales instead of Enterobacteriaceae.

The sentences in L47 & L48 have been changed. We googled the “carbapenemase-producing Enterobacteriaceae” and found it is a high-frequency word in numerous reports.

(2) L48. The drying up of the antibiotic discovery pipeline is NOT necessarily the reason to use colistin as a drug of last resort!

The sentence has been revised.

(3) The manuscript requires extensive English editing but has merit based on the strong compilation of data.

We have optimized and revised the writing of the whole article.

(4) I suggest the authors have some data on the cytotoxicity of AS alone, colistin alone, and both of them against eucaryotic cells (Caco-) and if possible determine IS (index selectivity). This additional experiment will strengthen the quality of the manuscript. The authors must also explain how to put such tri-therapy into practice.

The development of novel pharmaceutical dosage forms, pharmacokinetic, pharmacodynamic and safety analysis of the triple combination will be further conducted in our next study to provide a theoretical basis for the next clinical drug use. The discussion of potential toxicity of AS, colistin, EDTA and the triple combination have been added in line 318 to 337.

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 reviews for their thorough assessment of our manuscript and their constructive suggestions for further improvement. We are pleased that the reviewers recognise that “this work represents an important and substantive contribution” to the field of genome organization and gene transcription.

Reviewer 1

1) Does the CTCF degron substantially remove CTCF from the Mnx1/Shh TAD border? In prior AID-CTCF degron studies a considerable fraction of cohesin dependent TAD borders are retained upon CTCF removal. Moreover, CTCF sites at these retained borders still have clear ChIP-seq peaks - even though the protein is >95% depleted and scarcely detectable by western. Thus, while I suspect that the authors are correct that the shorter distance of the 35 kb border deletion contributes substantially to the increased crosstalk between the Mnx1 and Shh-enhancers, I suspect part of the reason for a lack of a similar effect in the CTCF degron is due to the known challenges in removing CTCF from this border. To argue that the border but not the CTCF is important, I think it would be helpful to show the CTCF signal is sufficiently lost in the degron by ChIP-seq and/or show that this TAD border has been lost by Hi-C. Alternatively, the authors could tone down this claim to something more conservative, as I did not find it to be presented as a key conclusion of the paper as a whole.

We used the CTCF-AID mESC line published by Nora et al (2017). In our previous manuscript (Kane et al., 2022) we presented the published Hi-C and CTCF-ChIP-seq data from these cells at the Shh TAD (Fig 2c of Kane et al) – reproduced below for the reviewer’s benefit. This shows the loss of insulation at the Shh/Mnx1 TAD boundary when CTCF is degraded, and the loss of CTCF ChIP-seq signal at this boundary.

• *

2) In my opinion, the authors' description of existing data for the importance of TAD borders in enhancer promoter regulation is not described in a sufficiently balanced and complete manner, and overall impression given by the text is that CTCF marked borders have little serious evidence for a role in developmental enhancer specificity and are maybe a cancer thing. This is doubly unfortunate, as it undermines the impact of the authors work in expanding our view of what TAD borders are in a regulatory sense, as well as presents an unbalanced view of work in the field. This is of course easily corrected. In particular, I recommend the following revisions: It is " depletion of CTCF has only a small effect on transcription in cell culture (Nora et al., 2017; Hsieh et al., 2022)." It should be clarified that there is only a small *acute * effect on transcription (in the first 6-12 hours), which may tell us more about the timescale at which promoters sample, integrate and respond to changes in their enhancer environment than about the roles of CTCF particularly. Notably, this degradation is *lethal*, it results in massive changes in transcription after 4 days, and I suspect the authors agree that this lethal affect arises from CTCF's role in transcription regulation (if you remove some key cytoskeletal protein or metabolic enzyme the primary cause of cell death is not transcriptional, but almost all the evidence for CTCF's vital role in the cell is linked in one way or another to transcription).

As suggested by the reviewer we have inserted the word “acute” into that sentence.

The discussion of TAD border deletions is more one-sided than ideal. I appreciate the discussion is usually even more unbalanced when presenting the opposite view in the literature - many works only cite the examples where border deletion does lead to ectopic expression and phenotypes. The current text presented a subset of these border deletion data in such a way as to give me the impression the authors are deeply skeptical that CTCF plays a role as an insulator of E-P interactions in a developmental context (rather than just as a weird cancer thing). For example: Pennacchio's lab has analyzed a series of TAD border deletions with more examples of both lethal effects and effects with no apparent phenotype 3

I appreciate that Bickmore and colleagues found quite phenotypically normal mice upon deletion of CTCF sites from Shh, but it might be balanced to still reference the work from Uishiki et al that indicate in humans the CTCF site does play a role in Shh - ZRS communication. As the authors are doubtless aware, Andrey and colleagues show a CTCF dependent enhancement of a sensitized ZRS enhancer. Zuin et al. in an elegant experiment in which an enhancer is mobilized to different distances away from its promoter using transposon induction, reported a complete lack of detection of enhancers mobilizing outside the TAD to activate gene expression. A balanced presentation of the data on CTCF role might include some discussion of the above. In light of these earlier works, the findings the authors report about border bypass are all the more surprising.

• *

We thank the reviewer for highlighting some of these studies, especially for drawing our attention to the interesting recent preprint from Chakraborty et al. (doi.org/10.1101/2024.08.03.606480), which we now discuss in the revised manuscript. * As suggested by the reviewer, we now also cite Ushiki et al., 2021 in the Introduction in the context of CTCF-associated phenotypes, rather than just in the Discussion as in the original submission. We already cited the work of Andrey and colleagues (Paliou et al). However, we chose not to cite the Pennacchio study, because the deletions used were large – all >10kb and some as large as 80kb. Therefore, we consider it highly likely that other regulatory sequences beyond CTCF sites themselves may have been deleted, complicating conclusions drawn about the function of the TAD boundaries per se. We have also chosen to focus our discussion on studies of enhancers in their native genomic locus, and predominantly in vivo analyses, rather than ectopic enhancer integrations (such as Zuin et al) in cell lines.*

4) By contrast, direct evidence for cross TAD interactions at endogenous loci has not to my knowledge been shown as clearly as described in the current manuscript. Recent work from Rocha and colleagues showed evidence that some enhancers upstream of Sox2 can pass ectopically induced boundaries. While recent work has described examples of 'TAD border bypass' at endogenous loci (e.g. for Pitx1 8, Hoxa regulation 9), these reports really just expand the view of regulatory boundaries rather than provide evidence against it. They invoke a 3D stacking of boundaries that allows boundary proximal enhancers and promoters to stack with (and so bypass) an intervening TAD boundary. Notably, in this view enhancers and promoters that lie away from the border of their respective TADs are still separate, and indeed intervening genes between distal enhancers for Pitx1 and Hoxa appear to follow these rules.2 Mnx1 and the Shh enhancers by contrast do not appear to be an example of border stacking. Given that Sox2 at least is also a TAD border, and the position of the bypassing enhancers is not precisely known in the work from Rocha, it is possible that that case is also an example of boundary stacking, which appears less likely in the case of Mnx1 (which does not appear to be at CTCF marked border, at least in mESCs).

• *

We thank the reviewer for highlighting some of these studies. We had already discussed the study from Rocha and colleagues (Chakraborty et al., 2023) and we had discussed the boundary stacking paper from Hung et al, (2024). However, based on the reviewer’s comment we now include a specific discussion about TAD boundary stacking and boundary proximal enhancer bypass, noting that Mnx1 is not close to a TAD boundary. This will become even more relevant in our planned revised manuscript where we will investigate possible Mnx1 activation by Shh enhancers (SBE2/3) located even further away from the Shh/Mnx1 TAD boundary.

Statistics: Some of the bar graphs quantifying the %-expressing cells do not obviously have associated n-values, as are some of the violin plots of the distances. I think all these bar graphs could also benefit from adding error bars (e.g. by bootstrapping from the sampled population). This will help the reader more easily appreciate how sampling error and sample size affect the variation seen in the plots.

We will add the n-values to all graphs. Regarding error bars, we think that showing the data from the two biological replicate separately is a better way to show the data reproducibility to the reader, than using boostrapping to estimate error bars.

Figures 2 and 3: I would have preferred the authors zoom in more on the FISH spots to help the reader appreciate the proximity. I do appreciate also seeing a field of more than 1 cell (to give some sense of the variability), but these images mostly have only 1 spot pair per panel, which is exceedingly small as they contain parts of more than 1 nucleus. There is also unnecessary white space in this figure that could have been used to show zoom in panels.

The same applies to the image panels in Figure 3 as for figure 2 - there is considerable unused whitespace, the image panels capture mostly a single nucleus and its pattern of DAPI dense heterochromatin (which isn't particularly relevant to the narrative) while the fluorescent spots that are the focus of the narrative are quite small. It is nice to have an example of the cell to see that this isn't just random background (that there is just one spot per cell) - in that sense though it's equally helpful to show its not just 1 cell in the field that has the signal-to-noise (SNR) shown. For this figure and the panels in figure 2, I'd recommend showing a zoom out showing ~3 nuclei with transcription foci (at least in the regions where the % transcribing is >60% it should be fine to have adjacent nuclei transcribing, for those where it is 10%, 1 of 3 nuclei transcribing in the image selected would also help get the sense of the data). These zoom out images would also give a sense of the SNR in the image, and then a zoom in where the FISH spots are sizable would make it easier to see the neighboring transcripts. Extended Data Fig 3 does a better job showing the context of the limb and then zooming in to an image where the RNA spots are appreciable. It looks like the resolution of the zoom in is lower, such that zooming in further on the spots in this data may not enhance the image.

• *

In response to the reviewer’s comment, we will present zoomed-out and zoomed-in images as suggested.

1. Figure 3 - DNA FISH It would be helpful to include a diagram indicated where the DNA FISH probes are located on the genome and their size in kb as an inset in the figure.

2. *

We will indicate the locations of DNA-FISH probes in a revised version of Figure 1a. Probe sizes are listed in the supplementary tables. We have now made this clearer in the legend to Figure 3.

• *

Reviewer 2

The authors claim that co-expression of Mnx1 and Shh in the foregut and lung buds is also driven by boundary crossing contacts with the MACS1 enhancer. However, the effect of the boundary deletion on the co-transcription of Shh and Mnx1 is only showed for the ZPA. In this sense I find potentially misleading the statement of the authors in the following paragraph: "In the ZPA, the foregut, and the lung buds, the majority of Mnx1 RNA-FISH signals are at alleles that show simultaneous signal for Shh nascent transcript from the same allele (closely apposed signals) (Fig. 2a, b and Extended Data Fig. 2a). In del 35 embryos, an even higher proportion of Mnx1 transcribing alleles also transcribe Shh (Fig. 2b,Extended Data Fig. 2a, Extended Data Table 3.). These data suggest that both the ZRS and MACS1 enhancers are able to simultaneously activate transcription at two gene loci on the same chromosome". In my opinion this phrasing implicitly extends the increase in Mnx1-Shh co-expressing nuclei observed in the ZPA of 35 del embryos to the expression of these two genes in the foregut and lung buds (driven by the MACS1 enhancer) while this effect has not been specifically addressed. In a previous work, the authors showed that boundary deletion does not impact Mnx1 expression in the foregut and lungs. It would be important to clarify whether more precise analysis in this study have led to different conclusions or, alternatively, appropriately discuss the results. Ideally the authors should analyse the effect of the 35 del allele in the foregut / lung buds or rephrase the statement about the sharing of the MACS1 enhancer. * *

The reviewer is correct that in our previous publication (Williamson et al., 2019) we did not detect Mnx1 expression in the lungs of 35kb del embryos. However, we only examined this by in situ hybridisation so we probably lacked the sensitivity to detect weak Mnx1 expression. In response to the reviewer’s comments, we now propose to do RNA FISH for transcription at Mnx1 in other tissues of 35kb del embryos.

The authors use the quantifications of nuclei co-expressing Mnx1 and Shh from the same allele as an indicator of simultaneous transcription of the two genes by the sharing of the enhancer as opposed to a model of alternate transcriptional bursts. However, I am concerned that the time scale at which looping and transcriptional bursts occur is at odds with the detection of nascent transcription in FISH experiments, thus not excluding that shifting of the enhancer from one promoter to the other could still result in detection of nascent RNA of the two genes in the same allele. In any case, following the argumentation of the authors, the fraction of nuclei expressing Mnx1 alone does not appear to be significantly different from those expressing Mnx1 and Shh, and the increase of Mnx1 expressing nuclei upon boundary deletion seem proportionally similar to the increase of Mnx1+/Shh+ nuclei. In my opinion, this makes it difficult to interpret the detection of Mnx1 alone or both Mnx1-Shh expression as a reflection of alternate looping and transcriptional burst from enhancer sharing. Determining whether the two promoters compete for the interaction with the enhancer or share it would require estimate whether in the 35 del homozygote embryos Shh expression is reduced compared to wts, as a result of the increased interaction of the ZRS with the enhancer. The authors claim that there are no differences in the % of cells expressing Shh upon boundary deletion but in my opinion measurement is not sufficient to estimate a change in transcriptional rate (frequency of bursting). Nascent mRNA level detection in single cells would allow to better asses competition or concomitant activation of the two gene. Not being an expert in the RAN FISH technique it is not clear to me whether fluorescence intensity could be used as an estimator of transcription. From the images of the authors, in some cases it seems that expression of Shh alone is higher than when both Shh and Mnx1 are transcribed from the same allele (Fig. 2a, left panel, Fig 2c left vs right panel. However, in other cases an opposite trend can be observed (Mnx1 intensity in Fig2a central vs right panel). Thus, a single nuclei PCR or RNAseq approach may be more suited for this assessment.

• *

We respectfully disagree with the reviewer. We argue that nascent RNA FISH, using probe pools that for the most part detect the introns of Shh and Mnx1, is a better measure of transcription bursting/frequency (on or off) than probe signal intensity and therefore is a measurement of transcription rate. Single nuclei PCR or RNAseq would not assay nascent transcription and would not distinguish between alleles.

Minor comments: 3. In the mESC model overexpressing the tZRS-VP64 construct, Shh and Mnx1 seem to be transcribed at similar rates compared to what observed in vivo (where only a minor fraction of Shh+ cells express Mnx1). Thus, despite the fact that TAD boundary deletion increases Mnx1, but not Shh, expression, the ZRS activity seems to more easily overcome the border in this context than in vivo. Could the authors comment on this interesting observation? May it relate to the insulation score of TAD boundaries in the mESCs compared to in vivo? Alternatively, could it reflect that combinatorial TF binding to an enhancer contribute to its directionality?

• *

*These are interesting speculations by the reviewer, but we would argue that it is hard to compare in vivo and in vitro experiments. For example, in the limb bud, the ZPA region where the ZRS is active cannot be distinguished morphologically from the surrounding mesenchymal cells, therefore it is likely that some nuclei that are just outside the ZPA may be included in the analysis. *

Overall, figure organization and clarity could be improved. For example, enlargement of RNA fish images in Fig. 1 could be enlarged (to the same size than the broad view image) and RNA FISH signal could be highlighted with arrowheads. Panel distribution could also be optimized.

• *

We will try to clarify these figures – see also response to reviewer 1 (point 6).

• *

Reviewer 3

There are a couple of claims and conclusions that are not fully supported by the data, and which I think could be resolved by rephrasing them and/or qualify them as preliminary or speculative. The authors often indicate co-expression as suggestive of co-regulation by a single enhancer, when in most cases this is not formally shown; such suggestion remains one among other possibilities. For instance, co-expression of Shh and Mnx1 in the developing bud is attributed to the ZRS enhancer, co-expression of Shh and Mnx1 in the foregut is attributed to MACS1 enhancer. Do the authors have any evidence that when deleting these enhancers, Mnx1 expression is abolished (or reduced) in the respective tissues?

If not, I think the following sentences need revision, because causality is implied by the way it is written but it is not formally shown (and the data could suggest other options too):

"However, we have previously identified that ZRS can also drive low level expression of Mnx1, located 150kb away in the adjacent TAD, in the developing limb bud (Williamson et al., 2019)." No genetic evidence is provided in Williamson et al. 2019

i) It is true that in Williamson et al., we did not provide genetic evidence that ZRS is the enhancer responsible for Mnx1 expression in the limb bud ZPA. However, there is no other known enhancer in biology with activity specific to the ZPA, and when the ZRS is deleted the ZPA no longer functions as a signaling centre for the limb bud. As a compromise, we have rephrased the indicated text to “However, we have previously identified that ZRS also appears to be able to drive low level expression of Mnx1, located 150kb away in the adjacent TAD, in the ZPA of the developing limb bud”.

"However, we also detect nascent transcription from Mnx1 in the Shh expressing portions of the developing ventral foregut and the lung bud of E10.5 embryos, an activity that is driven by the Shh MACS1 enhancer, located a further 100kb into the Shh TAD from ZRS (Sagai et al., 2017) and therefore able to induce transcription at Mnx1 across a TAD boundary from a distance of >260 kb (Fig. 1a)."

ii) We have modified the text to now read “However, we also detect nascent transcription from Mnx1 in the Shh expressing portions of the developing ventral foregut and the lung bud of E10.5 embryos, an activity that is likely to bedriven by the Shh MACS1 enhancer, located a further 100kb into the Shh TAD from ZRS”.

"These data suggest that both the ZRS and MACS1 enhancers are able to simultaneously activate transcription at two gene loci on the same chromosome."

iii) We have modified this statement to now read that these enhancers “may be able to simultaneously activate transcription at two gene loci on the same chromosome”.

"This is the first report of two endogenous mammalian genes transcribed simultaneously under the control of the same enhancer" (can the authors really claim this without genetic evidence, i.e., deleting the enhancer? Isn't that the golden standard in the field?).

iv) We stand by this claim, because we have been able to provide evidence in support of our observations in tissues, by using synthetic enhancer activation in cell culture where we can be absolutely be sure what the enhancer responsible for activation is.

"Therefore, the Shh ZRS enhancer can simultaneously activate transcription at two genes and across an intact, but porous, TAD boundary. See response (iv) above

"This is a consequence of ZRS-driven activation, not Mnx1 transcription per se."

v) We stand by this claim.

The mathematical model, even if simple, is very poorly described. In the results section, it is not easy to understand what the model takes into account, etc; it would be important for non-experts to understand as well what is at stake. In the methods section, it does not seem to be properly described; it is only stated "The association between the transcription of Shh and Mnx1 regulated by the same enhancer was done by linear modelling with binomial link function." Would this be enough to recreate / reproduce the same model? I am not a mathematician, but I suspect more details would be needed. * *

*We apologize if our approach was not clear. We used logistic regression not a mathematical model. We have now expanded the relevant Methods section to now read: *

“

“To test whether or not there is a tendency of coexpression between two loci on the same chromatid, only nuclei with exactly one signal of each locus are informative. For these nuclei, we scored how many had expression in cis and how many in trans. To assess whether there was chromatid-specific coexpression, we tested statistically whether there was an excess of nuclei showing expression in cis. We did this using logistic regression, a form of generalized linear regression model. More specifically, we tested, for each model, whether the model intercept was significantly different from zero by using the z-scaled test statistic returned by these models and converting it to a p-value.”

The authors claim that an enhancer working exclusively on one gene at a time would lead to a preference in individual expression - is this really the case? Could the authors show the expected scenarios for [one enhancer - two common targets] versus [two enhancers - two independent targets] and how this compares to the data?

• *

Our statistical analysis is restricted to the scenario of one enhancer acting on two genes (either simultaneously, or alternately). We do not test a two enhancers two target genes scenario because it is not relevant to our experimental analyses using synthetic activation of a single enhancer (with tZRS-Vp64, Extended Data Table 4).

1. The results obtained with the VP64 activation (activation of ZRS leads to increased expression of Mnx1) are used by the authors as another piece of evidence that ZRS controls Mnx1 - but could VP64 activation be inducing chromatin opening / enhanced accessibility and therefore increased expression across the TAD boundary? I am not sure the authors need to test this, but they should at least acknowledge other possibilities (in relation to point 1).

*We have previously shown (Benabdallah et al., 2019) that tal-VP64 activators alter chromatin structure (H3K27ac) in the Shh TAD only locally at the site of binding and at the Shh gene, and that this does not spread more generally. We have clarified this in the revised text. We also note that the effect of both the 35kb deletion and cohesin degradation on Mnx1 activation from the tZRSVp64 activator would not be consistent with a model of general chromatin opening/accessibility. The same argument applies to the DNA-FISH experiment (Fig 3) showing Mnx1 activation in the limb bud (ZPA) occurs specifically in the context of a compact chromatin conformation. *

"In the nuclei of pre-motor neurons, where Mnx1 expression is driven from its own proximal enhancers (Fig. 1a), Mnx-ZRS and Mnx1-Shh distances are not different between Mnx1 expressing and non-expressing alleles." The authors use this as an argument to claim that Mnx1 expression per se does not explain the distance differences observed in the limb bud - but can such comparisons of expression and distances between loci be made between different cell types? Is there enough evidence for this to be a valid assumption? If not, then the assumption should be explicitly presented.

• *

We believe that the reviewer is confused here. We are not suggesting that Mnx1 expression per se doesn’t explain the distance differences in the limb bud, rather that these distance differences in the limb bud associated with Mnx1 transcription do not occur in the pre-motor neurons where activation is not dependent on distal enhancers, particularly in the Shh TAD.

1. In Fig. 3b the authors show that shorter distances between the loci (Mnx1, Shh, ZRS) were associated with simultaneous transcription at Mnx1 and Shh, implying throughout that this would be associated with common activation by ZRS; but the shorter distances between the three loci are also associated with Mnx1 transcription alone. How is this explained?

2. *

*This is explained by the configuration of the Shh TAD and the general spatial proximity of Shh-ZRS in both expressing and non-expressing tissues due to the CTCF-mediated loop and that is apparent in Hi-C heat maps. *

1. The text could be revised to look out for "expression levels" versus "expression frequency" - in several instances the authors mention expression "levels" when they are referring to % of cells expressing a given gene, which would thus be more appropriate called "expression frequency"?

The reviewer makes an important point. In the revised manuscript we have removed all mention of “expression levels” and have replaced these with “ frequency”.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

SARS-CoV-2 infection induces syncytia formation, which promotes viral transmission. In this paper, the authors aimed to understand how host-derived inflammatory cytokines IL-1α/β combat SARS-CoV-2 infection.

Strengths:

First, they used a cell-cell fusion assay developed previously to identify IL-1α/β as the cytokines that inhibit syncytia formation. They co-cultured cells expressing the spike protein and cells expressing ACE2 and found that IL-1β treatment decreased syncytia formation and S2' cleavage.

Second, they investigated the IL-1 signaling pathway in detail, using knockouts or pharmacological perturbation to understand the signaling proteins responsible for blocking cell fusion. They found that IL-1 prevents cell-cell fusion through MyD88/IRAK/TRAF6 but not TAK1/IKK/NF-κB, as only knocking out MyD88/IRAK/TRAF6 eliminates the inhibitory effect on cell-cell fusion in response to IL-1β. This revealed that the inhibition of cell fusion did not require a transcriptional response and was mediated by IL-1R proximal signaling effectors.

Third, the authors identified RhoA/ROCK activation by IL-1 as the basis for this inhibition of cell fusion. By visualizing a RhoA biosensor and actin, they found a redistribution of RhoA to the cell periphery and cell-cell junctions after IL-1 stimulation. This triggered the formation of actin bundles at cell-cell junctions, preventing fusion and syncytia formation. The authors confirmed this molecular mechanism by using constitutively active RhoA and an inhibitor of ROCK.

Diverse Cell types and in vivo models were used, and consistent results were shown across diverse models. These results were convincing and well-presented.

Weaknesses:

As the authors point out in the discussion, whether IL-1-mediated RhoA activation is specific to viral infection or regulates other RhoA-regulated processes is unclear. We would also require high-magnification images of the subcellular organization of the cytoskeleton to appreciate the effect of IL-1 stimulation.

Thanks for the suggestions. We tested the role of IL-1β in other RhoA-regulated processes, and found that IL-1β-mediated RhoA activation also reduced cell migration in a cell scratch assay (see Author response image 1). We also provided high-magnification images in the revised Figures 4 and 5, as well as their respective figure supplements.

Author response image 1.

(A) Cell scratch assay images of HEK293T cells treated with PBS or IL-1β. (B) Quantification of cell migration in (A).

Reviewer #2 (Public Review):

Summary:

In this study, Zheng et al investigated the role of inflammatory cytokines in protecting cells against SARS-CoV-2 infection. They demonstrate that soluble factors in the supernatants of TLR-stimulated THP1 cells reduce fusion events between HEK293 cells expressing SARS-CoV-2 S protein and the ACE2 receptor. Using qRT-PCR and ELISA, they demonstrate that IL-1 cytokines are (not surprisingly) upregulated by TLR treatment in THP1 cells. Further, they convincingly demonstrate that recombinant IL-1 cytokines are sufficient to reduce cell-to-cell fusion mediated by the S protein. Using chemical inhibitors and CRISPR knock-out of key IL-1 receptor signaling components in HEK293 cells, they demonstrate that components of the myddosome (MYD88, IRAK1/4, and TRAF6) are required for fusion inhibition, but that downstream canonical signaling (i.e., TAK1 and NFKB activation) is not required. Instead, they provide evidence that IL-1-dependent non-canonical activation of RhoA/Rock is important for this phenotype. Importantly, the authors demonstrate that expression of a constitutively active RhoA alone is sufficient to inhibit fusion and that chemical inhibition of Rock could reverse this inhibition. The authors followed up these in vitro experiments by examining the effects of IL-1 on SARS-COV-2 infection in vivo and they demonstrate that recombinant IL-1 can reduce viral burden and lung pathogenesis in a mouse model of infection. However, the contribution of the RhoA/Rock pathway and inhibition of fusion to IL-1-mediated control of SARS-CoV-2 infection in vivo remains unclear.

Strengths:

(1) The bioluminescence cell-cell fusion assay provides a robust quantitative method to examine cytokine effects on viral glycoprotein-mediated fusion.

(2) The study identifies a new mechanism by which IL-1 cytokines can limit virus infection.

(3) The authors tested IL-1 mediated inhibition of fusion induced by many different coronavirus S proteins and several SARS-CoV-2 strains.

Weaknesses:

(1) The qualitative assay demonstrating S2 cleavage and IL-1 mediated inhibition of this phenotype is extremely variable across the data figures. Sometimes it appears like S2 cleavage (S2') is reduced, while in other figures immunoblots show that total S2 protein is decreased. Based on the proposed model the expectation would be that S2 abundance would be rescued when cleavage is inhibited.

In our present manuscript, IL-1-mediated changes of the full-length spike showed some variation between authentic SARS-CoV-2 infection model and HEK293T-S + HEK293T-ACE2 coculture model, while IL-1 inhibited S2’ cleavage accompanied by a reduction of S2 subunit in both models.

In the authentic SARS-CoV-2 infection model, we observed that IL-1 inhibited S2' cleavage accompanied with a reduction in both S2 subunit and full-length spike protein. This is likely because the S2 subunit and full-length spike protein in this model are not only from infected cells, but also from intracellular viral particles. IL-1 inhibited SARS-CoV-2 induced cell-cell fusion and reduced the viral load in host cells, therefore the abundance of S2 subunit and full-length spike proteins were both reduced.

In the HEK293T-based co-culture model, IL-1 inhibited S2' cleavage accompanied with a reduction in S2 subunit, while the full-length spike protein was more or less rescued. Based on our previous study, R685A and ΔRRAR spike mutants cannot generate the S2 subunit, but still generated S2′ fragment to induce cell-cell fusion, and the S2' fragment produced from R685A and ΔRRAR spike mutants were only slightly reduced compared to wild-type spike protein, suggesting that the S2' fragment is mainly derived from the full-length spike directly, and to a minimal extent from the S2 subunit (Fig. 4B and 4G, PMID: 34930824). Thus, inhibition of S2’ cleavage by IL-1 mainly rescued the full-length spike protein.

(2) The text referencing Figure 1H suggests that TLR-stimulated THP-1 cell supernatants "significantly" reduce syncytia, but image quantification and statistics are not provided to support this statement.

Thanks for pointing out this issue. We have provided fluorescence image quantification and statistics in the revised version of our manuscript (Figure 1D, Figure 1-figure supplement 1A, Figure 1H-1I, Figure 2H-2I, Figure 1-figure supplement 1D-1E, Figure 1-figure supplement 1H-1I, Figure 2-figure supplement 1C-1D, Figure 2-figure supplement 2B-2E, Figure 2-figure supplement 2G-2H, Figure 2-figure supplement 6A-6B, Figure 2-figure supplement 7F-7G).

(3) The authors conclude that because IL-1 accumulates in TLR2-stimulated THP1 monocyte supernatants, this cytokine accounts for the ability of these supernatants to inhibit cell-cell fusion. However, they do not directly test whether IL-1 is required for the phenotype. Inhibition of the IL-1 receptor in supernatant-treated cells would help support their conclusion.

Thanks for the suggestion. Accordingly, we performed experiment and found that IL-1RA treatment reduced the inhibitory effect of PGN-stimulated THP-1 cell culture supernatant on cell-cell fusion, suggesting that IL-1 is required for the inhibition. This result has been added in our revised manuscript (Figure 2J and Figure2-figure supplement 4C).

(4) Immunoblot analysis of IL-1 treated HEK293 cells suggests that this cytokine does not reduce the abundance of ACE2 or total S protein in cells. However, it is possible that IL-1 signaling reduces the abundance of these proteins on the cell surface, which would result in a similar inhibition of cell-cell fusion. The authors should confirm that IL-1 treatment of their cells does not change Ace2 or S protein on the cell surface.

Thanks for the suggestion. Accordingly, we applied Wheat Germ Agglutinin (WGA) to stain cell surface in HKE293T cells and observed that IL-1β treatment did not change ACE2 or Spike protein on the cell surface. This result has been added in our revised manuscript (Figure 5-figure supplement 3A-D).

(5) In Figure 5A, expression of constitutively active RhoA appears to have profound effects on how ACE2 runs by SDS-PAGE, suggesting that RhoA may have additional effects on ACE2 biology that might account for the decreased cell-cell fusion. This phenotype should be addressed in the text and explored in more detail.

Thanks for pointing out this. We also noticed that the occurrence of cell-cell fusion reduced the amount of ACE2, whereas inhibition of cell-cell fusion restored the ACE2 abundance. Take the original Figure 5A (revised Figure 4-figure supplement 2B) as example, the increased ACE2 protein should be attributed to the decreased cell-cell fusion upon RhoA-CA transfection, as Spike binding with ACE2 leads to clathrin- and AP2-dependent endocytosis, resulting in ACE2 degradation in the lysosome (PMID: 36287912).

In addition, we have examined the potential effect of RhoA-CA on ACE2, and found that RhoA-CA did not affect ACE2 expression, nor Spike binding to ACE2 (revised Figure 5-figure supplement 2E); it did not affect ACE2 distribution on cell surface either (revised Figure 5-figure supplement 2F and G).

(6) The experiments linking IL-1 mediated restriction of SARS-COV-2 fusion to the control of virus infection in vivo are incomplete. The reported data demonstrate that recombinant IL-1 can restrict virus replication in vivo, but they fall short of confirming that the in vitro mechanism described (reduced fusion) contributes to the control of SARS-CoV2 replication in vivo. A critical piece of data that is missing is the demonstration that the ROCK inhibitor phenocopies IL-1RA treatment of SARS-COV-2 infected mice (viral infection and pathology).

Thanks for this suggestion. Accordingly, we applied the ROCK inhibitor in vivo to confirm its role in SARS-CoV-2-infected mice, and found similar phenotype as the IL-1RA treatment experiment. That is to say, Y-26732 treatment prevented the formation of IL-1β-induced actin bundles at cell-cell junctions, thus promoted syncytia formation and further viral transmission in vivo (revised Figure 7).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I suggest providing single-channel images in a supplementary figure for the live-cell images in Figures 4 and 5. Higher magnification images would also help distinguish the subcellular details of the cytoskeleton organization.

Thanks for the suggestion. We have provided the single channel images and higher magnification images in the revised Figures 4 and 5, as well as their respective figure supplements.

In Figure 4, the authors showed that IL-1 activates RhoA and induces the accumulation of activated RhoA at the cell-cell junctions. They also showed that IL-1 promotes the formation of actin bundles at cell-cell junctions. However, the authors have not shown any connection between RhoA and actin yet, but in lines 263-264, they claim that actin bundle formation is induced by RhoA. Evidence for this part was shown in later results, but at this moment, it is lacking. The same applies to lines 282-284; I think this conclusion that IL-1-induced actin bundle formation is through the RhoA-ROCK pathway should come after showing how RhoA affects actin bundle formation at cell-cell junctions. To this end, I suggest moving Supplementary Figures S12B and S12D to the main figure, as they provide strong evidence of the IL-1-RhoA-ROCK-actin pathway.

We appreciate these valuable comments. As suggested, we have moved the respective supplementary figures to the main figures to support our findings in the revised manuscript (Figure 4E and Figure 4-figure supplement 2B; Figure 5C and Figure 5-figure supplement 2A), the text has also been adjusted accordingly.

Author response:

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

Reviewer #1 (Public review):

Summary:

In this study, Bu et al examined the dynamics of TRPV4 channel in cell overcrowding in carcinoma conditions. They investigated how cell crowding (or high cell confluence) triggers a mechano-transduction pathway involving TRPV4 channels in high-grade ductal carcinoma in situ (DCIS) cells that leads to large cell volume reduction (or cell volume plasticity) and proinvasive phenotype.

In vitro, this pathway is highly selective for highly malignant invasive cell lines derived from a normal breast epithelial cell line (MCF10CA) compared to the parent cell line, but not present in another triple-negative invasive breast epithelial cell line (MDA-MB-231). The authors convincingly showed that enhanced TRPV4 plasma membrane localization correlates with highgrade DCIS cells in patient tissue samples.

Specifically in invasive MCF10DCIS.com cells, they showed that overcrowding or overconfluence leads to a decrease in cell volume and intracellular calcium levels. This condition also triggers the trafficking of TRPV4 channels from intracellular stores (nucleus and potentially endosomes), to the plasma membrane (PM). When these over-confluent cells are incubated with a TRPV4 activator, there is an acute and substantial influx of calcium, attesting to the fact that there are a high number of TRPV4 channels present on the PM. Long-term incubation of these over-confluent cells with the TRPV4 activator results in the internalization of the PMlocalized TRPV4 channels.

In contrast, cells plated at lower confluence primarily have TRPV4 channels localized in the nucleus and cytosol. Long-term incubation of these cells at lower confluence with a TRPV4 inhibitor leads to the relocation of TRPV4 channels to the plasma membrane from intracellular stores and a subsequent reduction in cell volume. Similarly, incubation of these cells at low confluence with PEG 3000 (a hyperosmotic agent) promotes the trafficking of TRPV4 channels from intracellular stores to the plasma membrane.

Strengths:

The study is elegantly designed and the findings are novel. Their findings on this mechanotransduction pathway involving TRPV4 channels, calcium homeostasis, cell volume plasticity, motility, and invasiveness will have a great impact in the cancer field and are potentially applicable to other fields as well. Experiments are well-planned and executed, and the data is convincing. The authors investigated TRVP4 dynamics using multiple different strategies- overcrowding, hyperosmotic stress, and pharmacological means, and showed a good correlation between different phenomena.

Weaknesses:

A major emphasis in the study is on pharmacological means to relate TRPV4 channel function to the phenotype. I believe the use of genetic means would greatly enhance the impact and provide compelling proof for the involvement of TRPV4 channels in the associated phenotype.

In this regard, I wonder if siRNA-mediated knockdown of TRPV4 in over-confluent cells (or knockout) would lead to an increase in cell volume and normalize the intracellular calcium levels back to normal, thus ultimately leading to a decrease in cell invasiveness.

We greatly appreciate the positive feedback regarding the design of our study and the novelty of our findings. We also acknowledge the valuable suggestion to complement our pharmacological approaches with genetic manipulation of TRPV4.

In response to the comment regarding siRNA-mediated knockdown or knockout of TRPV4, we fully agree that this would further substantiate our findings. In the revised manuscript, we implemented shRNA targeting TRPV4 to investigate its functional effects on intracellular calcium level changes, cell volume plasticity, and invasiveness phenotypes, assessed through singlecell motility assays under cell crowding or hyperosmotic stress. These results have been incorporated into the revised manuscript, and detailed descriptions of these findings are included below.

Using the shRNA approach that resulted in ~50% reduction of TRPV4 expression

(Supplementary Figure 6A and 6B show TRPV4 expression levels via IF and immunoblots, respectively), we examined the effect of reduced TRPV4 on intracellular calcium levels in MCF10DCIS.com cells under normal density (ND) and stress conditions (confluent; Con and hyperosmotic; PEG) using Fluo-4 AM imaging (Fig. 4S-X). We found that shRNA TRPV4 slightly decreased calcium levels in ND cells, likely due to fewer active calcium channels at the plasma membrane resulting from lower TRPV4 expression (as shown in the summary plot in Fig. 4W). With fewer active calcium channels, cells treated with shRNA TRPV4 exhibited less reduction in intracellular calcium levels under cell crowding conditions compared to control cells. Additionally, hyperosmotic stress using PEG 300 induced smaller calcium spikes in shRNA cells compared to the significant spike observed in control cells. This reduced calcium response to Con and hyperosmotic stress in shRNA cells was reflected in the decreased cell volume reduction by PEG 300 shown in Fig. 4Y. Consequently, shRNA-mediated TRPV4 reduction impaired cell volume plasticity in MCF10DCIS.com cells and abolished the pro-invasive mechanotransduction capability involving cell volume reduction, as evidenced by no increase in cell motility (both cell diffusivity and directionality) under hyperosmotic conditions (Fig. 5H-J). These findings demonstrate the critical role of TRPV4 in conferring pro-invasive

mechanotransduction capability to MCF10DCIS.com cells through cell volume reduction.

Reviewer #2 (Public review):

Summary:

The metastasis poses a significant challenge in cancer treatment. During the transition from non-invasive cells to invasive metastasis cells, cancer cells usually experience mechanical stress due to a crowded cellular environment. The molecular mechanisms underlying mechanical signaling during this transition remain largely elusive. In this work, the authors utilize an in vitro cell culture system and advanced imaging techniques to investigate how non-invasive and invasive cells respond to cell crowding, respectively.

Strengths:

The results clearly show that pre-malignant cells exhibit a more pronounced reduction in cell volume and are more prone to spreading compared to non-invasive cells. Furthermore, the study identifies that TRPV4, a calcium channel, relocates to the plasma membrane both in vitro and in vivo (patient samples). Activation and inhibition of the TRPV4 channel can modulate the cell volume and cell mobility. These results unveil a novel mechanism of mechanical sensing in cancer cells, potentially offering new avenues for therapeutic intervention targeting cancer metastasis by modulating TRPV4 activity. This is a very comprehensive study, and the data presented in the paper are clear and convincing. The study represents a very important advance in our understanding of the mechanical biology of cancer.

Weaknesses:

However, I do think that there are several additional experiments that could strengthen the conclusions of this work. A critical limitation is the absence of genetic ablation of the TRPV4 gene to confirm its essential role in the response to cell crowding.

We are deeply grateful for the positive assessment of our study and its contribution to advancing our understanding of mechanical signaling in cancer progression. We also greatly appreciate the suggestion to incorporate genetic ablation experiments to further validate the role of TRPV4 in cell crowding responses.

As noted in our response to Reviewer #1, we employed an shRNA approach to investigate the functional effects of TRPV4 knockdown on intracellular calcium level changes, cell volume plasticity, and invasiveness phenotypes. We assessed these effects using Fluo-4 AM calcium assay, single-cell volume measurements, and single-cell motility assays under cell crowding or hyperosmotic stress. These results have been incorporated into the revised manuscript and are described in detail in our response to Reviewer #1's "weaknesses" comment.

Reducing TRPV4 expression levels by shRNA diminished mechanosensing intracellular calcium changes under cell crowding and hyperosmotic conditions using PEG 300 treatment. Furthermore, a significantly reduced cell volume plasticity was observed under hyperosmotic conditions in shRNA treated cells compared to control cells (Fig. 4S-X). This diminished mechanosensing capability abolished the pro-invasive mechanotransduction effect, as assessed by single cell motility under hyperosmotic conditions (Fig. 5H-J). These findings demonstrate the critical role of TRPV4 in conferring pro-invasive mechanotransduction capability to MCF10DCIS.com cells through cell volume reduction.

Reviewer #1 (Recommendations for the authors):

The way the results or discussion section is written. It was a little confusing for me to relate to some phenomena. For example, it is not clear how TRPV4 inhibition (due to overcrowding) leads to a decrease in intercellular calcium levels, especially when TRPV4 channels were intercellular (not on the PM) to begin with (in normal density (ND) conditions). Along the same lines, how GSK219 causes a dip in calcium levels in ND cells when TRPV4 channels are primarily intercellular (Figure 4E). If most of the TRPV4 channels that are translocated to the PM in response to cell crowding are in an inactive state, how do they confer enhanced cell volume plasticity relative to non-invasive cell lines?

Thank you very much for raising this important point. We fully agree with your concern and have significantly revised the manuscript to clarify this aspect. Specifically, we have emphasized that a modest level of TRPV4 channels are constitutively active at the plasma membrane in normal density (ND) cells. This is now discussed in detail in the context of Fig. 4:

Page 14: “Considering these factors, we hypothesized that cell crowding might inhibit calcium-permeant ion channels that are constitutively active at the plasma membrane, including TRPV4, which would then lower intracellular calcium levels and subsequently reduce cell volume via osmotic water movement.”

Page 16-17: “… However, the temporal profile of Fluo-4 intensity in Fig. 4E, which corresponds to the time points marked in Fig. 4D (t₁: baseline and t₂: dip), clearly shows the dip at t₂, indicated by ΔCa (the vertical dashed line between the dip and baseline). This modest Fluo-4 dip at t₂ represents the inhibition of activity by GSK219 on a small population of constitutively active TRPV4 channels at the plasma membrane under ND conditions.

In Con cells, 1 nM GSK219 caused a smaller dip in Fluo-4 intensity compared to the one observed in ND cells, with no subsequent changes. This is likely due to fewer constitutively active TRPV4 at the plasma membrane in Con cells than in ND cells. …These findings suggest that a substantial portion of TRPV4 channels relocated to the plasma membrane under cell crowding was inactive, and some constitutively active TRPV4 channels already present in the membrane became inactive as a result of cell crowding.”

'Internalization' might be a better word than 'uptake' in the following line in the results section

"...activating TRPV4 under cell crowding conditions triggered channel uptake, indicating that TRPV4 trafficking depended on the channel's activation status."

Thank you very much for this suggestion. As recommended, we replaced ‘uptake’ with internalization’ on page 18: 

“However, in Con cells, where a large number of inactive TRPV4 channels are likely located at the plasma membrane, GSK101 treatment notably reduced plasma membrane-associated TRPV4 in a dose-dependent manner through internalization (Fig. 4O, 4Q), consistent with previous findings65. These data suggest that plasma membrane TRPV4 levels were largely

regulated by the channel activity status. Specifically, channel activation led to the internalization of TRPV4, while channel inhibition promoted the relocation of TRPV4 to the plasma membrane.”

1. Out of curiosity:

2. Is there any information on what the intercellular TRPV4 channels are doing in the cytosol and in the nucleus? Is there any role of intercellular calcium stores in the proposed pathway?

We greatly appreciate this insightful question. Although we were unable to find studies specifically exploring the roles of cytosolic TRPV4, a recent study (Reference 74) identified a role for nuclear TRPV4 in regulating calcium within the nucleus. We speculate that when TRPV4 activity is severely impaired, such as with additional TRPV4 inhibition under cell crowding conditions, some TRPV4 channels may be redirected to the nucleus. This redistribution could help maintain nuclear calcium homeostasis.

This discussion is included on page 18 of the manuscript:

“These findings suggest that further TRPV4 inhibition under crowding conditions triggers a distinct trafficking alteration. Recent studies have implicated nuclear TRPV4 in regulating nuclear Ca2+ homeostasis and Ca2+-regulated transcription74. In light of this study and our findings, TRPV4 may relocate to the nucleus as a compensatory mechanism to maintain nuclear calcium regulation. This relocation could reflect an adaptive response to preserve calcium-dependent transcriptional programs or other nuclear processes essential for cell survival under mechanical stress.”

One recommendation is to add some explanation or some minor details for the convenience of the reader. For example:

At normal or lower confluence, cells show an acute large dip in intercellular calcium when an inhibitor is applied implying that there are a few TRPV4 channels on the PM and they are constitutively active.

Thank you very much for highlighting this important point and for the helpful suggestion to improve clarity. We have significantly revised the text associated with Fig. 4 to ensure this point is clear. Specifically, we have added the following explanation on page 16:

"This modest Fluo-4 dip at t2 represents the inhibition of activity by GSK219 on a small population of constitutively active TRPV4 channels at the plasma membrane under ND conditions."

Reviewer #2 (Recommendations for the authors):

(1) Figure 1. The authors frequently change the medium to prevent acidification in overconfluent cultures. A cell viability assay should be performed to ensure that the over-confluent cells remain healthy and viable during the experiments. There are commercial kits that can be easily used to quantify the number of viable cells and the extent of cell toxicity. The number of viable cells would provide a more reliable basis for comparison between normal density and overconfluent conditions.

Thank you very much for raising this important point. We have consistently observed that cell crowding does not induce significant cell death in MCF10DCIS.com cells. To address your recommendation, we performed a viability assay using propidium iodide (PI) to selectively stain dead cells and WGA-488 to stain all live cells. Cell death was quantified under normal density (ND) conditions and at 1, 3, 5, 7, and 10 days post-confluence.

Our results indicate that cells remain similarly viable post-confluence, with minimal cell death

(~1.5%) compared to ND cells (~0.75%). These findings are summarized in Supplementary Figure 2, demonstrating that over-confluent cultures remain healthy and viable during the experiments.

(2) Figure 2. To determine whether the reduction in cell volume is reversible, over-confluent cells can be further diluted back to normal density. Additionally, the reversibility of TRPV4 channel trafficking to the plasma membrane should be assessed under these conditions in IF experiments and cell surface biotinylation.

Thank you for this suggestion. We reseeded the previously overcrowded (OC) cells at normal density and observed that their TRPV4 distribution predominantly returned to being intracellular, with only modest plasma membrane localization, as shown by line analysis (Supplementary Figure 10A-C, page 13). Furthermore, their invasiveness decreased to levels comparable to the original normal density (ND) cells (Supplementary Figure 3C and 3E, page 6). These results demonstrate the reversibility of TRPV4 trafficking changes and the increase in invasiveness under mechanical stress.

Page 6. "The enhanced invasiveness of MCF10DCIS.com cells under cell crowding was largely reversible. When OC cells were reseeded at normal density for invasion assays, their invasive cell fraction decreased to approximately 15%, slightly lower (p = 0.012) than the initial value of around 24% (Suppl. Fig. 3C, 3E)."

Page 13. “We investigated whether TRPV4 relocation to the plasma membrane induced by cell crowding is reversible, as suggested by its impact on invasiveness (Suppl. Fig. 3E). To test this, previously OC MCF10DCIS.com cells were reseeded under ND conditions. We then assessed TRPV4 localization via immunofluorescence (IF) imaging to determine if most channels returned to the cytoplasm and could be relocated to the plasma membrane under mechanical stress, such as hyperosmotic conditions. Consistent with their initial ND state, reseeded ND MCF10DCIS.com cells displayed intracellular TRPV4 distribution (Suppl. Fig. 10A). Upon exposure to hyperosmotic stress (74.4 mOsm/Kg PEG300), TRPV4 was again relocated to the plasma membrane (Suppl. Fig. 10B). These findings, quantified through line analysis (Suppl. Fig. 10C), demonstrate that the mechanosensing response of MCF10DCIS.com cells is reversible.”

(3) Figure 3B. A control using intracellular proteins such as GAPDH or Tubulin is missing. Including this control would help exclude the possibility of cell rupture or compromised cell membranes in crowded environments, which is very common in a cell crowding environment.

Thank you very much for pointing this out. The control lanes (GAPDH) were already included in the full gel results shown in Supplementary Figure 5. For the immunoprecipitation and immunoblotting of surface-biotinylated cell lysates, we did not expect to detect GAPDH; however, some GAPDH signals were still observed. As shown for MCF10DCIS.com cells, less GAPDH was detected under OC conditions, but the immunoprecipitated samples displayed significantly higher levels of TRPV4 on the cell surface compared to ND cells (Supplementary Figure 5A). For the whole cell lysates, TRPV4 protein levels were comparable across different cell lines based on the immunoblot results, with consistent GAPDH signals serving as a loading control (Supplementary Figure 5B).

(4) Figure 4. To convincingly demonstrate TRPV4 relocation to the plasma membrane, IF should be performed under non-permeable conditions (i.e., without detergents like saponin). This approach ensures that only plasma membrane proteins are accessible to antibodies, reducing intracellular background. The same approach should be applied to Piezo1 and TfR.

Thank you for this suggestion. We observed that under non-permeable conditions, primary antibodies could still access intracellular proteins. To address this issue, we employed extracellular-binding TRPV4 antibodies to selectively detect TRPV4 relocation to the plasma membrane under hyperosmotic conditions (74.4 mOsm/kg PEG 300) in live MCF10DCIS.com cells, as shown in Supplementary Figure 9. These results clearly demonstrate the plasma membrane relocation of TRPV4 under hyperosmotic conditions, distinguishing it from control conditions. Unfortunately, we were unable to identify high-affinity extracellular-binding antibodies for Piezo1 and TfR. Nevertheless, our findings strongly support the mechanosensing plasma membrane relocation of TRPV4.

Essential Weakness:

Throughout the study, only TRPV4 inhibitors and activators were used to show that TRPV4 relocation is associated with intracellular calcium concentration and cell size changes. It is crucial to use TRPV4 KO or KD cells to confirm that the observed effects are specific to TRPV4 and not due to off-target effects on other proteins. Additionally, fusing a plasma membrane targeting sequence to TRPV4 to make a constitutive plasma membrane-localized construct could demonstrate the opposite effect.

Thank you very much for this important comment. As noted in our response to Reviewer #1, we employed an shRNA approach to investigate the functional effects of TRPV4 knockdown on intracellular calcium level changes, cell volume plasticity, and invasiveness phenotypes. We assessed these effects using Fluo-4 AM calcium assay, single-cell volume measurements, and single-cell motility assays under cell crowding or hyperosmotic stress. These results have been incorporated into the revised manuscript and are described in detail in our response to Reviewer #1's "weaknesses" comment.

Reducing TRPV4 expression levels by shRNA diminished mechanosensing intracellular calcium changes under cell crowding and hyperosmotic conditions using PEG 300 treatment. Furthermore, a significantly reduced cell volume plasticity was observed under hyperosmotic conditions in shRNA treated cells compared to control cells (Fig. 4S-X). This diminished mechanosensing capability abolished the pro-invasive mechanotransduction effect, as assessed by single cell motility under hyperosmotic conditions (Fig. 5H-J). These findings demonstrate the critical role of TRPV4 in conferring pro-invasive mechanotransduction capability to MCF10DCIS.com cells through cell volume reduction.

Minor Points:

The introduction section is poorly written; many results currently included in the introduction would be more appropriately placed in the discussion section. The long redundant introduction makes the article hard to read through.

Thank you very much for pointing this out. In the revised introduction, we have significantly reduced references to the results, streamlining the section to make it more concise and focused. This adjustment ensures the introduction is clearer and avoids redundancy, improving the readability of the manuscript.

Author response:

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

eLife Assessment

In an important fMRI study with an elegant experimental design and rigorous cross-decoding analyses, this work shows a solid dissociation between two parietal regions in visually processing actions. Specifically, aIPL is found to be sensitive to the causal effects of observed actions, while SPL is sensitive to the patterns of body motion involved in those actions. Additional analysis and explanation would help to determine the strength of evidence and the mechanistic underpinnings would benefit from closer consideration. Nevertheless, the work will be of broad interest to cognitive neuroscientists, particularly vision and action researchers.

We thank the editor and the reviewers for their assessment and their excellent comments and suggestions. We really believe they helped us to provide a stronger and more nuanced paper. In our revision, we addressed all points raised by the reviewers. Most importantly, we added a new section on a series of analyses to characterize in more detail the representations isolated by the action-animation and action-PLD cross-decoding. Together, these analyses strengthen the conclusion that aIPL and LOTC represent action effect structures at a categorical rather than specific level, that is, the type of change (e.g., of location or configuration) rather than the specific effect type (e.g. division, compression). SPL is sensitive to body-specific representations, specifically manuality (unimanual vs. bimanual) and movement kinematics. We also added several other analyses and addressed each point of the reviewers. Please find our responses below.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors report a study aimed at understanding the brain's representations of viewed actions, with a particular aim to distinguish regions that encode observed body movements, from those that encode the effects of actions on objects. They adopt a cross-decoding multivariate fMRI approach, scanning adult observers who viewed full-cue actions, pantomimes of those actions, minimal skeletal depictions of those actions, and abstract animations that captured analogous effects to those actions. Decoding across different pairs of these actions allowed the authors to pull out the contributions of different action features in a given region's representation. The main hypothesis, which was largely confirmed, was that the superior parietal lobe (SPL) more strongly encodes movements of the body, whereas the anterior inferior parietal lobe (aIPL) codes for action effects of outcomes. Specifically, region of interest analyses showed dissociations in the successful cross-decoding of action category across full-cue and skeletal or abstract depictions. Their analyses also highlight the importance of the lateral occipito-temporal cortex (LOTC) in coding action effects. They also find some preliminary evidence about the organisation of action kinds in the regions examined.

Strengths:

The paper is well-written, and it addresses a topic of emerging interest where social vision and intuitive physics intersect. The use of cross-decoding to examine actions and their effects across four different stimulus formats is a strength of the study. Likewise, the a priori identification of regions of interest (supplemented by additional full-brain analyses) is a strength.

Weaknesses:

I found that the main limitation of the article was in the underpinning theoretical reasoning. The authors appeal to the idea of "action effect structures (AES)", as an abstract representation of the consequences of an action that does not specify (as I understand it) the exact means by which that effect is caused, nor the specific objects involved. This concept has some face validity, but it is not developed very fully in the paper, rather simply asserted. The authors make the claim that "The identification of action effect structure representations in aIPL has implications for theories of action understanding" but it would have been nice to hear more about what those theoretical implications are. More generally, I was not very clear on the direction of the claim here. Is there independent evidence for AES (if so, what is it?) and this study tests the following prediction, that AES should be associated with a specific brain region that does not also code other action properties such as body movements? Or, is the idea that this finding -- that there is a brain region that is sensitive to outcomes more than movements -- is the key new evidence for AES?

Thank you for raising this important issue. We reasoned that AES should exist to support the recognition of perceptually variable actions, including those that we have never experienced before. To the best of our knowledge, there is only indirect evidence for the existence of AES, namely that humans effortlessly and automatically recognize actions (and underlying intentions and feelings) in movements of abstract shapes, as in the famous Heider and Simmel (1949) animations. As these animations do not contain any body posture or movement information at all, the only available cues are the spatiotemporal relations between entities and entity parts in the perceived scene. We think that the effortless and automatic attribution of actions to these stimuli points toward an evolutionary optimized mechanism to capture action effect structures from highly variable action instantiations (so general that it even works for abstract animations). Our study thus aimed to test for the existence of such a level of representation in the brain. We clarified this point in the introduction.

In our revised manuscript, we also revised our discussion of the implications of the finding of AES representations in the brain:

"The identification of action effect structure representations in aIPL and LOTC has implications for theories of action understanding: Current theories (see for review e.g. Zentgraf et al., 2011; Kemmerer, 2021; Lingnau and Downing, 2024) largely ignore the fact that the recognition of many goal-directed actions requires a physical analysis of the action-induced effect, that is, a state change of the action target. Moreover, premotor and inferior parietal cortex are usually associated with motor- or body-related processing during action observation. Our results, together with the finding that premotor and inferior parietal cortex are similarly sensitive to actions and inanimate object events (Karakose-Akbiyik et al., 2023), suggest that large parts of the 'action observation network' are less specific for body-related processing in action perception than usually thought. Rather, this network might provide a substrate for the physical analysis and predictive simulation of dynamic events in general (Schubotz, 2007; Fischer, 2024). In addition, our finding that the (body-independent) representation of action effects substantially draws on right LOTC contradicts strong formulations of a 'social perception' pathway in LOTC that is selectively tuned to the processing of moving faces and bodies (Pitcher and Ungerleider, 2021). The finding of action effect representation in right LOTC/pSTS might also offer a novel interpretation of a right pSTS subregion thought to specialized for social interaction recognition: Right pSTS shows increased activation for the observation of contingent action-reaction pairs (e.g. agent A points toward object; agent B picks up object) as compared to two independent actions (i.e., the action of agent A has no effect on the action of agent B) (Isik et al., 2017). Perhaps the activation reflects the representation of a social action effect - the change of an agent's state induced by someone else's action. Thus, the representation of action effects might not be limited to physical object changes but might also comprise social effects not induced by a physical interaction between entities. Finally, not all actions induce an observable change in the world. It remains to be tested whether the recognition of, e.g., communication (e.g. speaking, gesturing) and perception actions (e.g. observing, smelling) similarly relies on structural action representations in aIPL and LOTC"

On a more specific but still important point, I was not always clear that the significant, but numerically rather small, decoding effects are sufficient to support strong claims about what is encoded or represented in a region. This concern of course applies to many multivariate decoding neuroimaging studies. In this instance, I wondered specifically whether the decoding effects necessarily reflected fully five-way distinction amongst the action kinds, or instead (for example) a significantly different pattern evoked by one action compared to all of the other four (which in turn might be similar). This concern is partly increased by the confusion matrices that are presented in the supplementary materials, which don't necessarily convey a strong classification amongst action kinds. The cluster analyses are interesting and appear to be somewhat regular over the different regions, which helps. However: it is hard to assess these findings statistically, and it may be that similar clusters would be found in early visual areas too.

We agree that in our original manuscript, we did not statistically test what precisely drives the decoding, e.g., specific actions or rather broader categories. In our revised manuscript, we included a representational similarity analysis (RSA) that addressed this point. In short, we found that the action-animation decoding was driven by categorical distinctions between groups of actions (e.g. hit/place vs. the remaining actions) rather than a fully five-way distinction amongst all action kinds. The action-PLD decoding was mostly driven by , specifically manuality (unimanual vs. bimanual)) and movement kinematics; in left and right LOTC we found additional evidence for action-specific representations.

Please find below the new paragraph on the RSA:

"To explore in more detail what types of information were isolated by the action-animation and action-PLD cross-decoding, we performed a representational similarity analysis.

We first focus on the representations identified by the action-animation decoding. To inspect and compare the representational organization in the ROIs, we extracted the confusion matrices of the action-animation decoding from the ROIs (Fig. 5A) and compared them with different similarity models (Fig. 5B) using multiple regression. Specifically, we aimed at testing at which level of granularity action effect structures are represented in aIPL and LOTC: Do these regions encode the broad type of action effects (change of shape, change of location, ingestion) or do they encode specific action effects (compression, division, etc.)? In addition, we aimed at testing whether the effects observed in EVC can be explained by a motion energy model that captures the similarities between actions and animations that we observed in the stimulus-based action-animation decoding using motion energy features. We therefore included V1 in the ROI analysis. We found clear evidence that the representational content in right aIPL and bilateral LOTC can be explained by the effect type model but not by the action-specific model (all p < 0.005; two-sided paired t-tests between models; Fig. 5C). In left V1, we found that the motion energy model could indeed explain some representational variance; however, in both left and right V1 we also found effects for the effect type model. We assume that there were additional visual similarities between the broad types of actions and animations that were not captured by the motion energy model (or other visual models; see Supplementary Information). A searchlight RSA revealed converging results, and additionally found effects for the effect type model in the ventral part of left aIPL and for the action-specific model in the left anterior temporal lobe, left dorsal central gyrus, and right EVC (Fig. 5D). The latter findings were unexpected and should be interpreted with caution, as these regions (except right EVC) were not found in the action-animation cross-decoding and therefore should not be considered reliable (Ritchie et al., 2017). The motion energy model did not reveal effects that survived the correction for multiple comparison, but a more lenient uncorrected threshold of p = 0.005 revealed clusters in left EVC and bilateral posterior SPL.

To characterize the representations identified by the action-PLD cross-decoding, we used a manuality model that captures whether the actions were performed with both hands vs. one hand, an action-specific model as used in the action-animation RSA above, and a kinematics model that was based on the 3D kinematic marker positions of the PLDs (Fig. 6B). Since pSTS is a key region for biological motion perception, we included this region in the ROI analysis. The manuality model explained the representational variance in the parietal ROIs, pSTS, and LOTC, but not in V1 (all p < 0.002; two-sided paired t-tests between V1 and other ROIs; Fig. 6C). By contrast, the action-specific model revealed significant effects in V1 and LOTC, but not in pSTS and parietal ROIs (but note that effects in V1 and pSTS did not differ significantly from each other; all other two-sided paired t-tests between mentioned ROIs were significant at p < 0.0005). The kinematics model explained the representational variance in all ROIs. A searchlight RSA revealed converging results, and additionally found effects for the manuality model in bilateral dorsal/medial prefrontal cortex and in right ventral prefrontal cortex and insula (Fig. 6D).”

We also included an ROI covering early visual cortex (V1) in our analysis. While there was significant decoding for action-animation in V1, the representational organization did not substantially match the organization found in aIPL and LOTC: A cluster analysis revealed much higher similarity between LOTC and aIPL than between these regions and V1:

(please note that in this analysis we included the action-PLD RDMs as reference, and to test whether aIPL shows a similar representational organization in action-anim and action-PLD; see below)

Given these results, we think that V1 captured different aspects in the action-animation cross-decoding than aIPL and LOTC. We address this point in more detail in our response to the "Recommendations for The Authors".

Reviewer #2 (Public Review):

Summary:

This study uses an elegant design, using cross-decoding of multivariate fMRI patterns across different types of stimuli, to convincingly show a functional dissociation between two sub-regions of the parietal cortex, the anterior inferior parietal lobe (aIPL) and superior parietal lobe (SPL) in visually processing actions. Specifically, aIPL is found to be sensitive to the causal effects of observed actions (e.g. whether an action causes an object to compress or to break into two parts), and SPL to the motion patterns of the body in executing those actions.

To show this, the authors assess how well linear classifiers trained to distinguish fMRI patterns of response to actions in one stimulus type can generalize to another stimulus type. They choose stimulus types that abstract away specific dimensions of interest. To reveal sensitivity to the causal effects of actions, regardless of low-level details or motion patterns, they use abstract animations that depict a particular kind of object manipulation: e.g. breaking, hitting, or squashing an object. To reveal sensitivity to motion patterns, independently of causal effects on objects, they use point-light displays (PLDs) of figures performing the same actions. Finally, full videos of actors performing actions are used as the stimuli providing the most complete, and naturalistic information. Pantomime videos, with actors mimicking the execution of an action without visible objects, are used as an intermediate condition providing more cues than PLDs but less than real action videos (e.g. the hands are visible, unlike in PLDs, but the object is absent and has to be inferred). By training classifiers on animations, and testing their generalization to full-action videos, the classifiers' sensitivity to the causal effect of actions, independently of visual appearance, can be assessed. By training them on PLDs and testing them on videos, their sensitivity to motion patterns, independent of the causal effect of actions, can be assessed, as PLDs contain no information about an action's effect on objects.

These analyses reveal that aIPL can generalize between animations and videos, indicating that it is sensitive to action effects. Conversely, SPL is found to generalize between PLDs and videos, showing that it is more sensitive to motion patterns. A searchlight analysis confirms this pattern of results, particularly showing that action-animation decoding is specific to right aIPL, and revealing an additional cluster in LOTC, which is included in subsequent analyses. Action-PLD decoding is more widespread across the whole action observation network.

This study provides a valuable contribution to the understanding of functional specialization in the action observation network. It uses an original and robust experimental design to provide convincing evidence that understanding the causal effects of actions is a meaningful component of visual action processing and that it is specifically localized in aIPL and LOTC.

Strengths:

The authors cleverly managed to isolate specific aspects of real-world actions (causal effects, motion patterns) in an elegant experimental design, and by testing generalization across different stimulus types rather than within-category decoding performance, they show results that are convincing and readily interpretable. Moreover, they clearly took great care to eliminate potential confounds in their experimental design (for example, by carefully ordering scanning sessions by increasing realism, such that the participants could not associate animation with the corresponding real-world action), and to increase stimulus diversity for different stimulus types. They also carefully examine their own analysis pipeline, and transparently expose it to the reader (for example, by showing asymmetries across decoding directions in Figure S3). Overall, this is an extremely careful and robust paper.

Weaknesses:

I list several ways in which the paper could be improved below. More than 'weaknesses', these are either ambiguities in the exact claims made, or points that could be strengthened by additional analyses. I don't believe any of the claims or analyses presented in the paper show any strong weaknesses, problematic confounds, or anything that requires revising the claims substantially.

(1) Functional specialization claims: throughout the paper, it is not clear what the exact claims of functional specialization are. While, as can be seen in Figure 3A, the difference between action-animation cross-decoding is significantly higher in aIPL, decoding performance is also above chance in right SPL, although this is not a strong effect. More importantly, action-PLD cross-decoding is robustly above chance in both right and left aIPL, implying that this region is sensitive to motion patterns as well as causal effects. I am not questioning that the difference between the two ROIs exists - that is very convincingly shown. But sentences such as "distinct neural systems for the processing of observed body movements in SPL and the effect they induce in aIPL" (lines 111-112, Introduction) and "aIPL encodes abstract representations of action effect structures independently of motion and object identity" (lines 127-128, Introduction) do not seem fully justified when action-PLD cross-decoding is overall stronger than action-animation cross-decoding in aIPL. Is the claim, then, that in addition to being sensitive to motion patterns, aIPL contains a neural code for abstracted causal effects, e.g. involving a separate neural subpopulation or a different coding scheme. Moreover, if sensitivity to motion patterns is not specific to SPL, but can be found in a broad network of areas (including aIPL itself), can it really be claimed that this area plays a specific role, similar to the specific role of aIPL in encoding causal effects? There is indeed, as can be seen in Figure 3A, a difference between action-PLD decoding in SPL and aIPL, but based on the searchlight map shown in Figure 3B I would guess that a similar difference would be found by comparing aIPL to several other regions. The authors should clarify these ambiguities.

We thank the reviewer for this careful assessment. The observation of action-PLD cross-decoding in aIPL is indeed not straightforward to interpret: It could mean that aIPL encodes both body movements and action effect structures by different neural subpopulations. Or it could mean that representations of action effect structures were also activated by the PLDs, which lead to successful decoding in the action-PLD cross-decoding. Our revision allows a more nuanced view on this issue:

First, we included the results of a behavioral test show that PLDs at least weakly allow for recognition of the specific actions (see our response to the second comment), which in turn might activate action effect structure representations. Second, the finding that also the cross-decoding between animations and PLDs revealed effects in left and right aIPL (as pointed out by the reviewer in the second comment) supports the interpretation that PLDs have activated, to some extent, action effect structure representations.

On the other hand, if aIPL encodes only action-effect-structures, that were also captured in the action-PLD cross-decoding, we would expect that the RDMs in aIPL are similar for the action-PLD and action-animation cross-decoding. However, the cluster analysis (see our response to Reviewer 1 above) does not show this; rather, all action-PLD RDMs are representationally more similar with each other than with action-animation RDMs, specifically with regard to aIPL. In addition, the RSA revealed sensitivity to manuality and kinematics also in aIPL. This suggests that the action-PLD decoding in aIPL was at least partially driven by representations related to body movements.

Taken together, these findings suggest that aIPL encodes also body movements. In fact, we didn't want to make the strong claim that aIPL is selectively representing action effect structures. Rather, we think that our results show that aIPL and SPL are disproportionally sensitive to action effects and body movements, respectively. We added this in our revised discussion:

"The action-PLD cross-decoding revealed widespread effects in LOTC and parietal cortex, including aIPL. What type of representation drove the decoding in aIPL? One possible interpretation is that aIPL encodes both body movements (isolated by the action-PLD cross-decoding) and action effect structures (isolated by the action-animation cross-decoding). Alternatively, aIPL selectively encodes action effect structures, which have been activated by the PLDs. A behavioral test showed that PLDs at least weakly allow for recognition of the specific actions (Tab. S2), which might have activated corresponding action effect structure representations. In addition, the finding that aIPL revealed effects for the cross-decoding between animations and PLDs further supports the interpretation that PLDs have activated, at least to some extent, action effect structure representations.  On the other hand, if aIPL encodes only action effect structures, we would expect that the representational similarity patterns in aIPL are similar for the action-PLD and action-animation cross-decoding. However, this was not the case; rather, the representational similarity pattern in aIPL was more similar to SPL for the action-PLD decoding, which argues against distinct representational content in aIPL vs. SPL isolated by the action-PLD decoding. In addition, the RSA revealed sensitivity to manuality and kinematics also in aIPL, which suggests that the action-PLD decoding in aIPL was at least partially driven by representations related to body movements. Taken together, these findings suggest that aIPL encodes not only action effect structures, but also representations related to body movements. Likewise, also SPL shows some sensitivity to action effect structures, as demonstrated by effects in SPL for the action-animation and pantomime-animation cross-decoding. Thus, our results suggest that aIPL and SPL are not selectively but disproportionally sensitive to action effects and body movements, respectively."

A clarification to the sentence "aIPL encodes abstract representations of action effect structures independently of motion and object identity": Here we are referring to the action-animation cross decoding only; specifically, the fact that because the animations did not show body motion and concrete objects, the representations isolated in the action-animation cross decoding must be independent of body motion and concrete objects. This does not rule out that the same region encodes other kinds of representations in addition.

And another side note to the RSA: It might be tempting to test the "effects" model (distinguishing change of shape, change of location and ingest) also in the action-PLD multiple regression RSA in order to test whether this model explains additional variance in aIPL, which would point towards action effect structure representations. However, the "effect type" model is relatively strongly correlated with the "manuality" model (VIF=4.2), indicating that multicollinearity might exist. We therefore decided to not include this model in the RSA. However, we nonetheless tested the inclusion of this model and did not find clear effects for the "effects" model in aIPL (but in LOTC). The other models revealed largely similar effects as the RSA without the "effects" model, but the effects appeared overall noisier. In general, we would like to emphasize that an RSA with just 5 actions is not ideal because of the small number of pairwise comparisons, which increases the chance for coincidental similarities between model and neural RDMs. We therefore marked this analysis as "exploratory" in the article.

(2) Causal effect information in PLDs: the reasoning behind the use of PLD stimuli is to have a condition that isolates motion patterns from the causal effects of actions. However, it is not clear whether PLDs really contain as little information about action effects as claimed. Cross-decoding between animations and PLDs is significant in both aIPL and LOTC, as shown in Figure 4. This indicates that PLDs do contain some information about action effects. This could also be tested behaviorally by asking participants to assign PLDs to the correct action category. In general, disentangling the roles of motion patterns and implied causal effects in driving action-PLD cross-decoding (which is the main dependent variable in the paper) would strengthen the paper's message. For example, it is possible that the strong action-PLD cross-decoding observed in aIPL relies on a substantially different encoding from, say, SPL, an encoding that perhaps reflects causal effects more than motion patterns. One way to exploratively assess this would be to integrate the clustering analysis shown in Figure S1 with a more complete picture, including animation-PLD and action-PLD decoding in aIPL.

With regard to the suggestion to behaviorally test how well participants can grasp the underlying action effect structures: We indeed did a behavioral experiment to assess the recognizability of actions in the PLD stick figures (as well as in the pantomimes). In short, this experiment revealed that participants could not well recognize the actions in the PLD stick figures and often confused them with kinematically similar but conceptually different actions (e.g. breaking --> shaking, hitting --> swiping, squashing --> knitting). However, the results also show that it was not possible to completely eliminate that PLDs contain some information about action effects.

Because we considered this behavioral experiment as a standard assessment of the quality of the stimuli, we did not report them in the original manuscript. We now added an additional section to the methods that describes the behavioral experiments in detail:

"To assess how much the animations, PLD stick figures, and pantomimes were associated with the specific action meanings of the naturalistic actions, we performed a behavioral experiment. 14 participants observed videos of the animations, PLDs (without stick figures), and pantomimes in three separate sessions (in that order) and were asked to describe what kind of actions the animations depict and give confidence ratings on a Likert scale from 1 (not confident at all) to 10 (very confident). Because the results for PLDs were unsatisfying (several participants did not recognize human motion in the PLDs), we added stick figures to the PLDs as described above and repeated the rating for PLD stick figures with 7 new participants, as reported below.

A general observation was that almost no participant used verb-noun phrases (e.g. "breaking a stick") in their descriptions for all stimulus types. For the animations, the participants used more abstract verbs or nouns to describe the actions (e.g. dividing, splitting, division; Tab. S1). These abstract descriptions matched the intended action structures quite well, and participants were relatively confident about their responses (mean confidences between 6 and 7.8). These results suggest that the animations were not substantially associated with specific action meanings (e.g. "breaking a stick") but captured the coarse action structures. For the PLD stick figures (Tab. S2), responses were more variable and actions were often confused with kinematically similar but conceptually different actions (e.g. breaking --> shaking, hitting --> turning page, squashing --> knitting). Confidence ratings were relatively low (mean confidences between 3 and 5.1). These results suggest that PLD stick figures, too, were not substantially associated with specific action meanings and additionally did not clearly reveal the underlying action effect structures. Finally, pantomimes were recognized much better, which was also reflected in high confidence ratings (mean confidences between 8 and 9.2; Tab. S3). This suggests that, unlike PLD stick figures, pantomimes allowed much better to access the underlying action effect structures."

We also agree with the second suggestion to investigate in more detail the representational profiles in aIPL and SPL. We think that the best way to do so is the RSA that we reported above. However, to provide a complete picture of the results, we also added the whole brain maps and RDMs for the animation-pantomime, animation-PLD, pantomime-PLD, and action-pantomime to the supplementary information.

(3) Nature of the motion representations: it is not clear what the nature of the putatively motion-driven representation driving action-PLD cross-decoding is. While, as you note in the Introduction, other regions such as the superior temporal sulcus have been extensively studied, with the understanding that they are part of a feedforward network of areas analyzing increasingly complex motion patterns (e.g. Riese & Poggio, Nature Reviews Neuroscience 2003), it doesn't seem like the way in which SPL represents these stimuli are similarly well-understood. While the action-PLD cross-decoding shown here is a convincing additional piece of evidence for a motion-based representation in SPL, an interesting additional analysis would be to compare, for example, RDMs of different actions in this region with explicit computational models. These could be, for example, classic motion energy models inspired by the response characteristics of regions such as V5/MT, which have been shown to predict cortical responses and psychophysical performance both for natural videos (e.g. Nishimoto et al., Current Biology 2011) and PLDs (Casile & Giese Journal of Vision 2005). A similar cross-decoding analysis between videos and PLDs as that conducted on the fMRI patterns could be done on these models' features, obtaining RDMs that could directly be compared with those from SPL. This would be a very informative analysis that could enrich our knowledge of a relatively unexplored region in action recognition. Please note, however, that action recognition is not my field of expertise, so it is possible that there are practical difficulties in conducting such an analysis that I am not aware of. In this case, I kindly ask the authors to explain what these difficulties could be.

Thank you for this very interesting suggestion. We conducted a cross-decoding analysis that was based on the features of motion energy models as described in Nishimoto et al. (2011). Control analyses within each stimulus type revealed high decoding accuracies (animations: 100%, PLDs: 100%, pantomimes: 65%, actions: 55%), which suggests that the motion energy data generally contains information that can be detected by a classifier. However, the cross-decoding between actions and PLDs was at chance (20%), and the classification matrix did not resemble the neural RDMs. We also tested optical flow vectors as input to the decoding, which revealed similarly high decoding for the within-stimulus-type decoding (animations: 75%, PLDs: 100%, pantomimes: 65%, actions: 40%), but again at-chance decoding for action-PLD (20%), notably with a very different classification pattern:

Author response image 1.

Given these mixed results, we decided not to use these models for a statistical comparison with the neural action-PLD RDMs.

It is notable that the cross-decoding worked generally less well for decoding schemes that involve PLDs, which is likely due to highly different feature complexity of actions and PLDs: Naturalistic actions have much richer visual details, texture, and more complex motion cues. Therefore, motion energy features extracted from these videos likely capture a mixture of both fine-grained and broad motion information across different spatial frequencies. By contrast, motion energy features of PLDs are sparse and might not match the features of naturalistic actions. In a way, this was intended, as we were interested in higher-level body kinematics rather than lower-level motion features. We therefore decided to use a different approach to investigate the representational structure found in the action-PLD cross-decoding: As the PLDs were based on kinematic recordings of actions that were carried out in exactly the same manner as the naturalistic actions, we computed the dissimilarity of the 5 actions based on the kinematic marker positions. Specifically, we averaged the kinematic data across the 2 exemplars per PLD, vectorized the 3D marker positions of all time points of the PLDs (3 dimensions x 13 markers x 200 time points), computed the pairwise correlations between the 5 vectors, and converted the correlations into dissimilarity values by subtracting 1 - r. This RDM was then compared with the neural RDMs extracted from the action-PLD cross-decoding. This was done using a multiple regression RSA (see also our response to Reviewer 1's public comment 2), which allowed us to statistically test the kinematic model against other dissimilarity models: a categorical model of manuality (uni- vs. bimanual) and an action-specific model that discriminates each specific action from each other with equal distance.

This analysis revealed interesting results: the kinematic model explained the representational variance in bilateral SPL and (particularly right) pSTS as well as in right fusiform cortex and early visual cortex. The action-specific model revealed effects restricted to bilateral LOTC. The manuality model revealed widespread effects throughout the action observation network but not in EVC.

(4) Clustering analysis: I found the clustering analysis shown in Figure S1 very clever and informative. However, there are two things that I think the authors should clarify. First, it's not clear whether the three categories of object change were inferred post-hoc from the data or determined beforehand. It is completely fine if these were just inferred post-hoc, I just believe this ambiguity should be clarified explicitly. Second, while action-anim decoding in aIPL and LOTC looks like it is consistently clustered, the clustering of action-PLD decoding in SPL and LOTC looks less reliable. The authors interpret this clustering as corresponding to the manual vs. bimanual distinction, but for example "drink" (a unimanual action) is grouped with "break" and "squash" (bimanual actions) in left SPL and grouped entirely separately from the unimanual and bimanual clusters in left LOTC. Statistically testing the robustness of these clusters would help clarify whether it is the case that action-PLD in SPL and LOTC has no semantically interpretable organizing principle, as might be the case for a representation based entirely on motion pattern, or rather that it is a different organizing principle from action-anim, such as the manual vs. bimanual distinction proposed by the authors. I don't have much experience with statistical testing of clustering analyses, but I think a permutation-based approach, wherein a measure of cluster robustness, such as the Silhouette score, is computed for the clusters found in the data and compared to a null distribution of such measures obtained by permuting the data labels, should be feasible. In a quick literature search, I have found several papers describing similar approaches: e.g. Hennig (2007), "Cluster-wise assessment of cluster stability"; Tibshirani et al. (2001) "Estimating the Number of Clusters in a Data Set Via the Gap Statistic". These are just pointers to potentially useful approaches, the authors are much better qualified to pick the most appropriate and convenient method. However, I do think such a statistical test would strengthen the clustering analysis shown here. With this statistical test, and the more exhaustive exposition of results I suggested in point 2 above (e.g. including animation-PLD and action-PLD decoding in aIPL), I believe the clustering analysis could even be moved to the main text and occupy a more prominent position in the paper.

With regard to the first point, we clarified in the methods that we inferred the 3 broad action effect categories after the stimulus selection: "This categorization was not planned before designing the study but resulted from the stimulus selection."

Thank you for your suggestion to test more specifically the representational organization in the action-PLD and action-animation RDMs. However, after a careful assessment, we decided to replace the cluster analysis with an RSA. We did this for two reasons:

First, we think that RSA is a better (and more conventional) approach to statistically investigate the representational structure in the ROIs (and in the whole brain). The RSA allowed us, for example, to specifically test the mentioned distinction between unimanual and bimanual actions, and to test it against other models, i.e., a kinematic model and an action-specific model. This indeed revealed interesting distinct representational profiles of SPL and LOTC.

Second, we learned that the small number of items (5) is generally not ideal for cluster analyses (absolute minimum for meaningful interpretability is 4, but to form at least 2-3 clusters a minimum of 10-15 items is usually recommended). A similar rule of thumb applies to methods to statistically assess the reliability of cluster solutions (e.g., Silhouette Scores, Cophenetic Correlation Coefficient, Jaccard Coefficient). Finally, the small number of items is not ideal to run a permutation test because the number of unique permutations (for shuffling the data labels: 5! = 30) is insufficient to generate a meaningful null distribution. We therefore think it is best to discard the cluster analysis altogether. We hope you agree with this decision.

(5) ROI selection: this is a minor point, related to the method used for assigning voxels to a specific ROI. In the description in the Methods (page 16, lines 514-24), the authors mention using the MNI coordinates of the center locations of Brodmann areas. Does this mean that then they extracted a sphere around this location, or did they use a mask based on the entire Brodmann area? The latter approach is what I'm most familiar with, so if the authors chose to use a sphere instead, could they clarify why? Or, if they did use the entire Brodmann area as a mask, and not just its center coordinates, this should be made clearer in the text.

We indeed used a sphere around the center coordinate of the Brodmann areas. This was done to keep the ROI sizes / number of voxels constant across ROIs. Since we aimed at comparing the decoding accuracies between aIPL and SPL, we thereby minimized the possibility that differences in decoding accuracy between ROIs are due to ROI size differences. The approach of using spherical ROIs is a quite well established practice that we are using in our lab by default (e.g. Wurm & Caramazza, NatComm, 2019; Wurm & Caramazza, NeuroImage, 2019; Karakose, Caramazza, & Wurm, NatComm, 2023). We clarified that we used spherical ROIs to keep the ROI sizes constant in the revised manuscript.

Reviewer #3 (Public Review):

This study tests for dissociable neural representations of an observed action's kinematics vs. its physical effect in the world. Overall, it is a thoughtfully conducted study that convincingly shows that representations of action effects are more prominent in the anterior inferior parietal lobe (aIPL) than the superior parietal lobe (SPL), and vice versa for the representation of the observed body movement itself. The findings make a fundamental contribution to our understanding of the neural mechanisms of goal-directed action recognition, but there are a couple of caveats to the interpretation of the results that are worth noting:

(1) Both a strength of this study and ultimately a challenge for its interpretation is the fact that the animations are so different in their visual content than the other three categories of stimuli. On one hand, as highlighted in the paper, it allows for a test of action effects that is independent of specific motion patterns and object identities. On the other hand, the consequence is also that Action-PLD cross-decoding is generally better than Action-Anim cross-decoding across the board (Figure 3A) - not surprising because the spatiotemporal structure is quite different between the actions and the animations. This pattern of results makes it difficult to interpret a direct comparison of the two conditions within a given ROI. For example, it would have strengthened the argument of the paper to show that Action-Anim decoding was better than Action-PLD decoding in aIPL; this result was not obtained, but that could simply be because the Action and PLD conditions are more visually similar to each other in a number of ways that influence decoding. Still, looking WITHIN each of the Action-Anim and Action-PLD conditions yields clear evidence for the main conclusion of the study.

The reviewer is absolutely right: Because the PLDs are more similar to the actions than the animations, a comparison of the effects of the two decoding schemes is not informative. As we also clarified in our response to Reviewer 2, we cannot rule out that the action-PLD decoding picked up information related to action effect structures. Thus, the only firm conclusion that we can draw from our study is that aIPL and SPL are disproportionally sensitive to action effects and body movements, respectively. We clarified this point in our revised discussion.

(2) The second set of analyses in the paper, shown in Figure 4, follows from the notion that inferring action effects from body movements alone (i.e., when the object is unseen) is easier via pantomimes than with PLD stick figures. That makes sense, but it doesn't necessarily imply that the richness of the inferred action effect is the only or main difference between these conditions. There is more visual information overall in the pantomime case. So, although it's likely true that observers can more vividly infer action effects from pantomimes vs stick figures, it's not a given that contrasting these two conditions is an effective way to isolate inferred action effects. The results in Figure 4 are therefore intriguing but do not unequivocally establish that aIPL is representing inferred rather than observed action effects.

We agree that higher decoding accuracies for Action-Pant vs. Action-PLD and Pant-PLD could also be due to visual details (in particular of hands and body) that are more similar in actions and pantomimes relative to PLDs. However, please note that for this reason we included also the comparison of Anim-Pant vs. Anim-PLD. For this comparison, visual details should not influence the decoding. We clarified this point in our revision.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

It struck me that there are structural distinctions amongst the 5 action kinds that were not highlighted and may have been unintentional. Specifically, three of the actions are "unary" in a sense: break(object), squash(object), hit(object). One is "binary": place(object, surface), and the fifth (drink) is perhaps ternary - transfer(liquid, cup, mouth)? Might these distinctions be important for the organization of action effects (or actions generally)?

This is an interesting aspect that we did not think of yet. We agree that for the organization of actions (and perhaps action effects) this distinction might be relevant. One issue we noticed, however, is that for the animations the suggested organization might be less clear, in particular for "drink" as ternary, and perhaps also for "place" as binary. Thus, in the action-animation cross-decoding, this distinction - if it exists in the brain - might be harder to capture. We nonetheless tested this distinction. Specifically, we constructed a dissimilarity model (using the proposed organization, valency model hereafter) and tested it in a multiple regression RSA against an effect type model and two other models for specific actions (discriminating each action from each other with the same distance) and motion energy (as a visual control model). This analysis revealed no effects for the "valency" model in the ROI-based RSA. Also a searchlight analysis revealed no effects for this model. Since we think that the valency model is not ideally suited to test representations of action effects (using data from the action-animation cross-decoding) and to make the description of the RSA not unnecessarily complicated, we decided to not include this model in the final RSA reported in the manuscript.

In general, I found it surprising that the authors treated their LOTC findings as surprising or unexpected. Given the long literature associating this region with several high-level visual functions related to body perception, action perception, and action execution, I thought there were plenty of a priori reasons to investigate the LOTC's behaviour in this study. Looking at the supplementary materials, indeed some of the strongest effects seem to be in that region.

(Likewise, classically, the posterior superior temporal sulcus is strongly associated with the perception of others' body movements; why not also examine this region of interest?)

One control analysis that would considerably add to the strength of the authors' conclusions would be to examine how actions could be cross-decoded (or not) in the early visual cortex. Especially in comparisons of, for example, pantomime to full-cue video, we might expect a high degree of decoding accuracy, which might influence the way we interpret similar decoding in other "higher level" regions.

We agree that it makes sense to also look into LOTC and pSTS, and also EVC. We therefore added ROIs for these regions: For EVC and LOTC we used the same approach based on Brodmann areas as for aIPL and SPL, i.e., we used BA 17 for V1 and BA 19 for LOTC. For pSTS, we defined the ROI based on a meta analysis contrast for human vs. non-human body movements (Grobras et al., HBM 2012). Indeed we find that the strongest effects (for both action effect structures and body movements) can be found in LOTC. We also found effects in EVC that, at least for the action-animation cross-decoding, are more difficult to interpret. To test for a coincidental visual confound between actions and animations, we included a control model for motion energy in the multiple regression RSA, which could indeed explain some of the representational content in V1. However, also the effect type model revealed effects in V1, suggesting that there were additional visual features that caused the action-animation cross-decoding in V1. Notably, as pointed out in our response to the Public comments, the representational organization in V1 was relatively distinct from the representational organization in aIPL and LOTC, which argues against the interpretation that effects in aIPL and LOTC were driven by the same (visual) features as in V1.

Regarding the analyses reported in Figure 4: wouldn't it be important to also report similar tests for SPL?

In the analysis of implied action effect structures, we focused on the brain regions that revealed robust effects for action-animation decoding in the ROI and the searchlight analysis, that is, aIPL and SPL. However, we performed a whole brain conjunction analysis to search for other brain regions that show a profile for implied action effect representation. This analysis (that we forgot to mention in our original manuscript; now corrected) did not find evidence for implied action effect representations in SPL.

However, for completeness, we also added a ROI analysis for SPL. This analysis revealed a surprisingly complex pattern of results: We observed stronger decoding for Anim-Pant vs. Anim-PLD, whereas there were no differences for the comparisons of Action-Pant with Action-PLD and Pant-PLD:

This pattern of results is not straightforward to explain: First, the equally strong decoding for Action-Pant, Action-PLD, and Pant-PLD suggests that SPL is not substantially sensitive to body part details. Rather, the decoding relied on the coarse body part movements, independently of the specific stimulus type (action, pantomime, PLD). However, the stronger difference between Anim-Pant and Anim-PLD suggests that SPL is also sensitive to implied AES. This appears unlikely, because no effects (in left aIPL) or only weak effects (in right SPL) were found for the more canonical Action-Anim cross-decoding. The Anim-Pant cross-decoding was even stronger than the Action-Anim cross-decoding, which is counterintuitive because naturalistic actions contain more information than pantomimes, specifically with regard to action effect structures. How can this pattern of results be interpreted? Perhaps, for pantomimes and animations, not only aIPL and LOTC but also SPL is involved in inferring (implied) action effect structures. However, for this conclusion, also differences for the comparison of Action-Pant with Action-PLD and for Action-Pant with Pant-PLD should be found. Another non-mutually exclusive interpretation is that both animations and pantomimes are more ambiguous in terms of the specific action, as opposed to naturalistic actions. For example, the squashing animation and pantomime are both ambiguous in terms of what is squashed/compressed, which might require additional load to infer both the action and the induced effect. The increased activation of action-related information might in turn increase the chance for a match between neural activation patterns of animations and pantomimes.

In any case, these additional results in SPL do not question the effects reported in the main text, that is, disproportionate sensitivity for action effect structures in right aIPL and LOTC and for body movements in SPL and other AON regions. The evidence for implied action effect structures representation in SPL is mixed and should be interpreted with caution.

We added this analysis and discussion as supplementary information.

Statistical arguments that rely on "but not" are not very strong, e.g. "We found higher cross-decoding for animation-pantomime vs. animation-PLD in right aIPL and bilateral LOTC (all t(23) > 3.09, all p < 0.0025; one-tailed), but not in left aIPL (t(23) = 0.73, p = 0.23, one-tailed)." Without a direct statistical test between regions, it's not really possible to support a claim that they have different response profiles.

Absolutely correct. Notably, we did not make claims about different profiles of the tested ROIs with regard to implied action effect representations. But of course it make sense to test for differential profiles of left vs. right aIPL, so we have added a repeated measures ANOVA to test for an interaction between TEST (animation-pantomime, animation-PLD) and ROI (left aIPL, right aIPL), which, however, was not significant (F(1,23)=3.66, p = 0.068). We included this analysis in the revised manuscript.

Reviewer #2 (Recommendations for The Authors):

(1) I haven't found any information about data and code availability in the paper: is the plan to release them upon publication? This should be made clear.

Stimuli, MRI data, and code are deposited at the Open Science Framework (https://osf.io/am346/). We included this information in the revised manuscript.

(2) Samples of videos of the stimuli (or even the full set) would be very informative for the reader to know exactly what participants were looking at.

We have uploaded the full set of stimuli on OSF (https://osf.io/am346/).

(3) Throughout the paper, decoding accuracies are averaged across decoding directions (A->B and B->A). To my knowledge, this approach was proposed in van den Hurk & Op de Beeck (2019), "Generalization asymmetry in multivariate cross-classification: When representation A generalizes better to representation B than B to A". I believe it would be fair to cite this paper.

Absolutely, thank you very much for the hint. We included this reference in our revised manuscript.

(4) Page 3, line 70: this is a very nitpicky point, but "This suggests that body movements and the effects they induce are at least partially processed independently from each other." is a bit of an inferential leap from "these are distinct aspects of real-world actions" to "then they should be processed independently in the brain". The fact that a distinction exists in the world is a prerequisite for this distinction existing in the brain in terms of functional specialization, but it's not in itself a reason to believe that functional specialization exists. It is a reason to hypothesize that the specialization might exist and to test that hypothesis. So I think this sentence should be rephrased as "This suggests that body movements and the effects they induce might be at least partially processed independently from each other.", or something to that effect.

Your reasoning is absolutely correct. We revised the sentence following your suggestion.

(5) Page 7, line 182: the text says "stronger decoding for action-animation vs. action-PLD" (main effect of TEST), which is the opposite of what can be seen in the figure. I assume this is a typo?

Thanks for spotting this, it was indeed a typo. We corrected it: “…stronger decoding for action-PLD vs. action-animation cross-decoding..”

(6) Page 7, Figure 3B: since the searchlight analysis is used to corroborate the distinction between aIPL and SPL, it would be useful to overlay the contours of these ROIs (and perhaps LOTC as well) on the brain maps.

We found that overlaying the contours of the ROIs onto the decoding searchlight maps would make the figure too busy, and the contours would partially hide effects. However, we added a brain map with all ROIs in the supplementary information.

(7) Page 9, Figure 4A: since the distinction between the significant difference between anim-pant and anim-PLD is quite relevant in the text, I believe highlighting the lack of difference between the two decoding schemes in left aIPL (for example, by writing "ns") in the figure would help guide the reader to see the relevant information. It is generally quite hard to notice the absence of something.

We added “n.s.” to the left aIPL in Fig. 4A.

(8) Page 11, line 300: "Left aIPL appears to be more sensitive to the type of interaction between entities, e.g. how a body part or an object exerts a force onto a target object" since the distinction between this and the effect induced by that interaction" is quite nuanced, I believe a concrete example would clarify this for the reader: e.g. I guess the former would involve a representation of the contact between hand and object when an object is pushed, while the latter would represent only the object's displacement following the push?

Thank you for the suggestion. We added a concrete example: “Left aIPL appears to be more sensitive to the type of interaction between entities, that is, how a body part or an object exerts a force onto a target object (e.g. how a hand makes contact with an object to push it), whereas right aIPL appears to be more sensitive to the effect induced by that interaction (the displacement of the object following the push).”

(9) Page 12, line 376: "Informed consent, and consent to publish, was obtained from the participant in Figure 2." What does this refer to? Was the person shown in the figure both a participant in the study and an actor in the stimulus videos? Since this is in the section about participants in the experiment, it sounds like all participants also appeared in the videos, which I guess is not the case. This ambiguity should be clarified.

Right, the statement sounds misleading in the “Participants” section. We rephrased it and moved it to the “Stimuli” section: “actions…were shown in 4 different formats: naturalistic actions, pantomimes, point light display (PLD) stick figures, and abstract animations (Fig. 2; informed consent, and consent to publish, was obtained from the actor shown in the figure).”

(10) Page 15, line 492: Here, "within-session analyses" are mentioned. However, these analyses are not mentioned in the text (only shown in Figure S2) and their purpose is not clarified. I imagine they were a sanity check to ensure that the stimuli within each stimulus type could be reliably distinguished. This should be explained somewhere.

We clarified the purpose of the within session decoding analyses in the methods section: "Within-session decoding analyses were performed as sanity checks to ensure that for all stimulus types, the 5 actions could be reliably decoded (Fig. S2)."

(11) Page 20, Figure S1: I recommend using the same color ranges for the two decoding schemes (action-anim and action-PLD) in A and C, to make them more directly comparable.

Ok, done.

Reviewer #3 (Recommendations For The Authors):

(1) When first looking at Figure 1B, I had a hard time discerning what action effect was being shown (I thought maybe it was "passing through") Figure 2 later clarified it for me, but it would be helpful to note in the caption that it depicts breaking.

Thank you for the suggestion. Done.

(2) It would be helpful to show an image of the aIPL and SPL ROIs on a brain to help orient readers - both to help them examine the whole brain cross-decoding accuracy and to aid in comparisons with other studies.

We added a brain map with all ROIs in the supplementary information.

(3) Line 181: I'm wondering if there's an error, or if I'm reading it incorrectly. The line states "Moreover, we found ANOVA main effects of TEST (F(1,24)=33.08, p=7.4E-06), indicating stronger decoding for action-animation vs. action-PLD cross-decoding..." But generally, in Figure 3A, it looks like accuracy is lower for Action-Anim than Action-PLD in both hemispheres.

You are absolutely right, thank you very much for spotting this error. We corrected the sentence: “…stronger decoding for action-PLD vs. action-animation cross-decoding..”

(4) It might be useful to devote some more space in the Introduction to clarifying the idea of action-effect structures. E.g., as I read the manuscript I found myself wondering whether there is a difference between action effect structures and physical outcomes in general... would the same result be obtained if the physical outcomes occurred without a human actor involved? This question is raised in the discussion, but it may be helpful to set the stage up front.

We clarified this point in the introduction:

In our study, we define action effects as induced by intentional agents. However, the notion of action effect structures might be generalizable to physical outcomes or object changes as such (e.g. an object's change of location or configuration, independently of whether the change is induced by an agent or not).

(5) Regarding my public comment #2, it would perhaps strengthen the argument to run the same analysis in the SPL ROIs. At least for the comparison of Anim-Pant with Anim-PLD, the prediction would be no difference, correct?

The prediction would indeed be that there is no difference for the comparison of Anim-Pant with Anim-PLD, but also for the comparison of Action-Pant with Action-PLD and for Action-Pant with Pant-PLD, there should be no difference. As explained in our response to the public comment #2, we ran a whole brain conjunction (Fig. 4B) to test for the combination of these effects and did not find SPL in this analysis. However, we did found differences for Anim-Pant vs. Anim-PLD, which is not straightforward to interpret (see our response to your public comment #2 for a discussion of this finding).

Author response:

Public Reviews:

Reviewer #1 (Public review):

When you search for something, you need to maintain some representation (a "template") of that target in your mind/brain. Otherwise, how would you know what you were looking for? If your phone is in a shocking pink case, you can guide your attention to pink things based on a target template that includes the attribute 'pink'. That guidance should get you to the phone pretty effectively if it is in view. Most real-world searches are more complicated. If you are looking for the toaster, you will make use of your knowledge of where toasters can be. Thus, if you are asked to find a toaster, you might first activate a template of a kitchen or a kitchen counter. You might worry about pulling up the toaster template only after you are reasonably sure you have restricted your attention to a sensible part of the scene.

Zhou and Geng are looking for evidence of this early stage of guidance by information about the surrounding scene in a search task. They train Os to associate four faces with four places. Then, with Os in the scanner, they show one face - the target for a subsequent search. After an 8 sec delay, they show a search display where the face is placed on the associated scene 75% of the time. Thus, attending to the associated scene is a good idea. The questions of interest are "When can the experimenters decode which face Os saw from fMRI recording?" "When can the experimenters decode the associated scene?" and "Where in the brain can the experimenters see evidence of this decoding? The answer is that the face but not the scene can be read out during the face's initial presentation. The key finding is that the scene can be read out (imperfectly but above chance) during the subsequent delay when Os are looking at just a fixation point. Apparently, seeing the face conjures up the scene in the mind's eye.

This is a solid and believable result. The only issue, for me, is whether it is telling us anything specifically about search. Suppose you trained Os on the face-scene pairing but never did anything connected to the search. If you presented the face, would you not see evidence of recall of the associated scene? Maybe you would see the activation of the scene in different areas and you could identify some areas as search specific. I don't think anything like that was discussed here.

You might also expect this result to be asymmetric. The idea is that the big scene gives the search information about the little face. The face should activate the larger useful scene more than the scene should activate the more incidental face, if the task was reversed. That might be true if the finding is related to a search where the scene context is presumed to be the useful attention guiding stimulus. You might not expect an asymmetry if Os were just learning an association.

It is clear in this study that the face and the scene have been associated and that this can be seen in the fMRI data. It is also clear that a valid scene background speeds the behavioral response in the search task. The linkage between these two results is not entirely clear but perhaps future research will shed more light.

It is also possible that I missed the clear evidence of the search-specific nature of the activation by the scene during the delay period. If so, I apologize and suggest that the point be underlined for readers like me.

We will respond to this question by acknowledging that the reviewer is right in that the delay period activation of the scene is not necessarily search-specific. We will then discuss how this possibility affects the interpretation of our results and what kind of studies would need to be conducted in order to fully establish a causal link between delay period activity and visual search performance. We will also discuss the literature on cued attention and situate our work within the context of these other studies that have used similar task paradigms to infer attentional processes. Finally, we will discuss the interpretation of delay period activity in PPA and IFJ.

Reviewer #2 (Public review):

Summary:

This work is one of the best instances of a well-controlled experiment and theoretically impactful findings within the literature on templates guiding attentional selection. I am a fan of the work that comes out of this lab and this particular manuscript is an excellent example as to why that is the case. Here, the authors use fMRI (employing MVPA) to test whether during the preparatory search period, a search template is invoked within the corresponding sensory regions, in the absence of physical stimulation. By associating faces with scenes, a strong association was created between two types of stimuli that recruit very specific neural processing regions - FFA for faces and PPA for scenes. The critical results showed that scene information that was associated with a particular cue could be decoded from PPA during the delay period. This result strongly supports the invoking of a very specific attentional template.

Strengths:

There is so much to be impressed with in this report. The writing of the manuscript is incredibly clear. The experimental design is clever and innovative. The analysis is sophisticated and also innovative. The results are solid and convincing.

Weaknesses:

I only have a few weaknesses to point out.

This point is not so much of a weakness, but a further test of the hypothesis put forward by the authors. The delay period was long - 8 seconds. It would be interesting to split the delay period into the first 4seconds and the last 4seconds and run the same decoding analyses. The hypothesis here is that semantic associations take time to evolve, and it would be great to show that decoding gets stronger in the second delay period as opposed to the period right after the cue. I don't think this is necessary for publication, but I think it would be a stronger test of the template hypothesis.

We will conduct the suggested analysis. Depending on the outcome, we will include it in supplemental materials or the main text.

Type in the abstract "curing" vs "during."

We will fix this.

It is hard to know what to do with significant results in ROIs that are not motivated by specific hypotheses. However, for Figure 3, what are the explanations for ROIs that show significant differences above and beyond the direct hypotheses set out by the authors?

We will address how each of the ROIs wdas selected based on the use of a priori networks as masks with ROIs as sub-parcels. We will explain why specific ROIs were associated with the strongest hypotheses but how the entire networks are relevant and related to existing literatures on attentional control and working memory. This content will be included in the introduction and discussion sections.

Reviewer #3 (Public review):

The manuscript contains a carefully designed fMRI study, using MVPA pattern analysis to investigate which high-level associate cortices contain target-related information to guide visual search. A special focus is hereby on so-called 'target-associated' information, that has previously been shown to help in guiding attention during visual search. For this purpose the author trained their participants and made them learn specific target-associations, in order to then test which brain regions may contain neural representations of those learnt associations. They found that at least some of the associations tested were encoded in prefrontal cortex during the cue and delay period.

The manuscript is very carefully prepared. As far as I can see, the statistical analyses are all sound and the results integrate well with previous findings.

I have no strong objections against the presented results and their interpretation.

Thank you.

Author response:

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

Reviewer #1:

Comment#1: Ren et al developed a novel computational method to investigate cell evolutionary trajectory for scRNA-seq samples. This method, MGPfact, estimates pseudotime and potential branches in the evolutionary path by explicitly modeling the bifurcations in a Gaussian process. They benchmarked this method using synthetic as well as real-world samples and showed superior performance for some of the tasks in cell trajectory analysis. They further demonstrated the utilities of MGPfact using single-cell RNA-seq samples derived from microglia or T cells and showed that it can accurately identify the differentiation timepoint and uncover biologically relevant gene signatures. Overall I think this is a useful new tool that could deliver novel insights for the large body of scRNA-seq data generated in the public domain. The manuscript is written in a logical way and most parts of the method are well described.

Thank you for reviewing our manuscript and for your positive feedback on MGPfact. We are pleased that you find it useful for identifying differentiation timepoints and uncovering gene signatures. We will continue to refine MGPfact and explore its applications across diverse datasets. Your insights are invaluable, and we appreciate your support.

Comment#2: Some parts of the methods are not clear. It should be outlined in detail how pseudo time T is updated in Methods. It is currently unclear either in the description or Algorithm 1.

Thanks to the reviewers' comments. We've added a description of how pseudotime T is obtained between lines 138 and 147 in the article. In brief, the pseudotime of MGPfact is inferred through Gaussian process regression on the downsampled single-cell transcriptomic data. Specifically, T is treated as a continuous variable representing the progression of cells through the differentiation process. We describe the relationship between pseudotime and expression data using the formula:

Where f(T) is a Gaussian Process (GP) with covariance matrix S, and Ɛ represents the error term. The Gaussian process is defined as:

Where is the variance set to 1e-6.

During inference, we update the pseudotime by maximizing the posterior likelihood. Specifically, the posterior distribution of pseudotime T can be represented as:

Where is the likelihood function of the observed data Y*, and is the prior distribution of the Gaussian process. This posterior distribution integrates the observed data with model priors, enabling inference of pseudotime and trajectory simultaneously. Due to the high autocorrelation of  in the posterior distribution, we use Adaptive Metropolis within Gibbs (AMWG) sampling (Roberts and Rosenthal, 2009; Tierney, 1994). Other parameters are estimated using the more efficient SLICE sampling technique (Neal, 2003).

Comment#3: There should be a brief description in the main text of how synthetic data were generated, under what hypothesis, and specifically how bifurcation is embedded in the simulation.

Thank you for the reviewers' comments. We have added descriptions regarding the synthetic dataset in the methods section. The revised content is from line 487 to 493:

“The synthetic datasets were generated using four simulators: dyngen (Saelens et al., 2019), dyntoy (Saelens et al., 2019), PROSSTT (Papadopoulos et al., 2019), and Splatter (Zappia et al., 2017), each modeling different trajectory topologies such as linear, branching, and cyclic. Splatter simulates branching events by setting expression states and transition probabilities, dyntoy generates random expression gradients to reflect dynamic changes, and dyngen focuses on complex branching structures within gene regulatory networks.”

Comment#4: Please explain what the abbreviations mean at their first occurrence.

We appreciate the reviewers' feedback. We have thoroughly reviewed the entire manuscript and made sure that all abbreviations have had their full forms provided upon their first occurrence.

Comment#5: In the benchmark analysis (Figures 2/3), it would be helpful to include a few trajectory plots of the real-world data to visualize the results and to evaluate the accuracy.

We appreciate the reviewer's feedback. To more clearly demonstrate the performance of MGPfact, we selected three representative cases from the dataset for visual comparison. These cases represent different types of trajectory structures: linear, bifurcation, and multifurcation. The revised content is between line 220 and 226.

As shown in Supplementary Fig. 5, it is evident that MGPfact excels in capturing main developmental paths and identifying key bifurcation points. In the linear trajectory structure, MGPfact accurately predicted the linear structure without bifurcation events, showing high consistency with the ground truth (overall\=0.871). In the bifurcation trajectory structure, MGPfact accurately captured the main bifurcation event (overall\=0.636). In the multifurcation trajectory structure, although MGPfact predicted only one bifurcation point, its overall structure remains close to the ground truth, as evidenced by its high overall score (overall\=0.566). Overall, MGPfact demonstrates adaptability and accuracy in reconstructing various types of trajectory structures.

Comment#6: It is not clear how this method selects important genes/features at bifurcation. This should be elaborated on in the main text.

Thanks to the reviewers' comments. To enhance understanding, we've added detailed descriptions of gene selection in the main text and appendix, specifically from lines 150 to 161. In brief, MGPfact employs a Gaussian process mixture model to infer cell fate trajectories and identify independent branching events. We calculate load matrices using formulas 1 and 14 to assess each gene's contribution to the trajectories. Genes with an absolute weight greater than 0.05 are considered predominant in specific branching processes. Subsequently, SCENIC (Aibar et al., 2017; Bravo González-Blas et al., 2023) analysis was conducted to further infer the underlying regulons and annotate the biological processes of these genes.

Comment#7: It is not clear how survival analysis was performed in Figure 5. Specifically, were critical confounders, such as age, clinical stage, and tumor purity controlled?

To evaluate the predictive and prognostic impacts of the selected genes, we utilized the Cox multivariate regression model, where the effects of relevant covariates, including age, clinical stage, and tumor purity, were adjusted. We then conducted the Kaplan-Meier survival analysis again to ensure the reliability of the results. The revisions mainly include the following sections:

(1) We modified the description of adjusting for confounding factors in the survival analysis, from line 637 to 640:

“To adjust for possible confounding effects, the relevant clinical features including age, sex and tumor stage were used as covariates. The Cox regression model was implemented using R-4.2 package “survival”. And we generated Kaplan-Meier survival curves based on different classifiers to illustrate differences in survival time and report the statistical significance based on Log-rank test.”

(2) We updated the images in the main text regarding the survival analysis, including Fig. 5a-b, Fig. 6c, and Supplementary Fig. 8e.

Comment#8: I recommend that the authors perform some sort of 'robustness' analysis for the consensus tree built from the bifurcation Gaussian process. For example, subsample 80% of the cells to see if the bifurcations are similar between each bootstrap.

We appreciate the reviewers' feedback. We performed a robustness analysis of the consensus tree using 100 training datasets. This involved sampling the original data at different proportions, and then calculating the topological similarity between the consensus trajectory predictions of MGPfact and those without sampling, using the Hamming-Ipsen-Mikhailov (HIM ) metric. A higher score indicates greater robustness. The relevant figure is in Supplementary Fig. 4, and the description is in the main text from line 177 to 182.

The results indicate that the consensus trajectory predictions based on various sampling proportions of the original data maintain a high topological similarity with the unsampled results (HIM_mean=0.686). This demonstrates MGPfact’s robustness and generalizability under different data conditions, hence the capability of capturing bifurcative processes in the cells’ trajectory.

Reviewer #2:

Comment#1: The authors present MGPfact^XMBD, a novel model-based manifold-learning framework designed to address the challenges of interpreting complex cellular state spaces from single-cell RNA sequences. To overcome current limitations, MGPfact^XMBD factorizes complex development trajectories into independent bifurcation processes of gene sets, enabling trajectory inference based on relevant features. As a result, it is expected that the method provides a deeper understanding of the biological processes underlying cellular trajectories and their potential determinants. MGPfact^XMBD was tested across 239 datasets, and the method demonstrated similar to slightly superior performance in key quality-control metrics to state-of-the-art methods. When applied to case studies, MGPfact^XMBD successfully identified critical pathways and cell types in microglia development, validating experimentally identified regulons and markers. Additionally, it uncovered evolutionary trajectories of tumor-associated CD8+ T cells, revealing new subtypes with gene expression signatures that predict responses to immune checkpoint inhibitors in independent cohorts. Overall, MGPfact^XMBD represents a relevant tool in manifold learning for scRNA-seq data, enabling feature selection for specific biological processes and enhancing our understanding of the biological determinants of cell fate.

Thank you for your thoughtful review of our manuscript. We are thrilled to hear that you find MGPfact^XMBD beneficial for exploring cellular evolutionary paths in scRNA-seq data. Your insights are invaluable, and we look forward to incorporating them to further enrich our study. Thank you once again for your support and constructive feedback.

Comment#2: How the methods compare with existing Deep Learning based approaches such as TIGON is a question mark. If a comparison would be possible, it should be conducted; if not, it should be clarified why.

We appreciate the reviewer's comments. We have added a comparison with the sctour (Li, 2023) and TIGON methods (Sha, 2024).

It is important to note that the encapsulation and comparison of MGPfact are based on traditional differentiation trajectory construction. Saelens et al. established a systematic evaluation framework that categorizes differentiation trajectory structures into topological subtypes such as linear, bifurcation, multifurcation, graph, and tree, focusing on identifying branching structures in the cell differentiation process (Saelens et al., 2019). The sctour and TIGON methods mentioned by the reviewer are primarily used for estimating RNA velocity, focusing on continuous temporal evolution rather than explicit branching structures, and do not explicitly model branches. Therefore, we considered the predictions of these two methods as linear trajectories and compared them with MGPfact. While scTour explicitly estimates pseudotime, TIGON uses the concept of "growth," which is analogous to pseudotime, so we made the necessary adaptations.

Author response image 1 show that within this framework, compared to scTour (overall_mean=0.448) and TIGON (overall_mean=0.263), MGPfact still maintains a relatively high standard (overall_mean=0.534). This indicates that MGPfact has a significant advantage in accurately capturing branching structures in cell differentiation, especially in applications where explicit modeling of branches is required.

Author response image 1.

Comparison of MGPfact with scTour and TIGON in trajectory inference performance across 239 test datasets. a. Overall scores; b.F1_branches; c.HIM; d. cor_dist; e. wcor_features. All results are color-coded based on the trajectory types, with the black line representing the mean value. The “Overall” assessment is calculated as the geometric mean of all four metrics.

Comment#3: Missing Methods:

- The paper lacks a discussion of Deep Learning approaches for bifurcation analysis. e.g. scTour, Tigon.

- I am missing comments on methods such CellRank, and alternative approaches to delineate a trajectory.

We thank the reviewer for these comments.

(1) As mentioned in response to Comments#2, the scTour and TIGON methods are primarily used for estimating RNA velocity, focusing on continuous temporal evolution rather than explicit branching structures, and they do not explicitly model branches. We consider the predictions of these two methods as linear trajectories and compare them with MGPfact. The relevant description and discussion have been addressed in the response.

(2) We have added a description of RNA velocity estimation methods (scTour, TIGON, CellRank) in the introduction section. The revised content is from line 66 to 71:

“Moreover, recent studies based on RNA velocity has provided insights into cell state transitions. These methods measure RNA synthesis and degradation rates based on the abundance of spliced and unspliced mRNA, such as CellRank (Lange et al., 2022). Nevertheless, current RNA velocity analyses are still unable to resolve cell-fates with complex branching trajectory. Deep learning methods such as scTour (Li, 2023) and TIGON (Sha, 2024) circumvent some of these limitations, offering continuous state assumptions or requiring prior cell sampling information.”

Comment#4: Impact of MURP:

The rationale for using MURP is well-founded, especially for trajectory definition. However, its impact on the final results needs evaluation.

How does the algorithm compare with a random subselection of cells or the entire cell set?

Thank you for the comments. We fully agree that MURP is crucial in trajectory prediction. As a downsampling method, MURP is specifically designed to address noise issues in single-cell data by dividing the data into several subsets, thereby maximizing noise reduction while preserving the main structure of biological variation (Ren et al., 2022). In MGPfact, MURP typically reduces the data to fewer than 100 downsampled points, preserving the core biological structure while lowering computational complexity. To assess MURP's impact, we conducted experiments by randomly selecting 20, 40, 60, 80, and 100 cells for trajectory inference. These results were mapped back to the original data using the KNN graph structure for final predictions, which were then compared with the MURP downsampling results. Supplementary results can be found in Supplementary Fig. 3, with additional descriptions in the main text from line 170 to 176.

The results indicate that trajectory inference using randomly sampled cells has significantly lower prediction accuracy compared to that using MURP. This is particularly evident in branch assignment (F1_branches) and correlation cor_dist, where the average levels decrease by 20.5%-64.9%. In contrast, trajectory predictions using MURP for downsampling show an overall score improvement of 5.31%-185%, further highlighting MURP's role in enhancing trajectory inference within MGPfact.

Comment#5: What is the impact of the number of components selected?

Thank you for the comments. In essence, MGPfact consists of two main steps: 1) trajectory inference; 2) calculation of factorized scores and identification of high-weight genes. After step 1, MGPfact estimates parameters such as pseudotime T and bifurcation points B.  In step 2, we introduce a rotation matrix to obtain factor scores W_l  for each trajectory l by rotating Y*.

For all trajectories,

where e_l  is the error term for the -th trajectory. The number of features in Y* must match the dimensions of the rotation matrix R to ensure the factorized score matrix W contains factor scores for  trajectories, achieving effective feature representation and interpretation in the model.

Additionally, to further illustrate the impact of the number of principal components (PCs) on model performance in step 1, we conducted additional experiments. We used 3 PCs as the default and adjusted the number to evaluate changes from this baseline. As shown in Author response image 2, setting the number of PCs to 1 significantly decreases the overall performance score (overall_mean=0.363), as well as the wcor_features and wcor_dist metrics.  In contrast, increasing the number of PCs does not significantly affect the metrics. It ought to be mentioned that number of components used should be determined by the intrinsic biological characteristics of the cell fate-determination. Our experiment based on a limited number of datasets may not represent more complex scenarios in other cell types.

Author response image 2.

Robustness testing of the number of MURP PCA components on 100 training datasets. With the number of principal components (PCs) set to 3 by default; we tested the impact of different number of components (1-10) on the prediction results. In all box plots, the asterisk represents the mean value, while the whiskers extend to the farthest data points within 1.5 times the interquartile range. Significance is denoted as follows: not annotated indicates non-significant; * P < 0.05; ** P < 0.01; *** P < 0.001; two-sided paired Student’s T-tests.

Comment#6: Please comment on the selection of the kernel functions (rbf and polynomial) and explain why other options were discarded.

Thank you for the comments. We have added a description regarding the selection of radial basis functions and polynomial kernels in lines 126-130. As the reviewers mentioned, the choice of kernel functions is crucial in the MGPfact analysis pipeline for constructing the covariance matrix of the Gaussian process. We selected the radial basis function (RBF) kernel and the polynomial kernel to balance capturing data complexity and computational efficiency. The RBF kernel is chosen for its ability to effectively model smooth functions and capture local variations in the data, making it well-suited to the continuous and smooth characteristics of biological processes; its hyperparameters offer modeling flexibility. The polynomial kernel is used to capture more complex nonlinear relationships between input features, with its hyperparameters also allowing further customization of the model. In contrast, other complex kernels, such as Matérn or spectral kernels, were omitted due to their interpretability challenges and the risk of overfitting with limited data. However, as suggested by the reviewers, we will consider and test the impact of other kernel functions on the covariance matrix of the Gaussian process and their role in trajectory inference in our subsequent phases of algorithm design.

Comment#7: What is the impact of the Pseudotime method used initially? This section should be expanded with clear details on the techniques and parameters used in each analysis.

We are sorry for the confusion. We've added a description of how pseudotime T is obtained between line 138 and 147 in the main text. And the specific hyperparameters involved in the model and their prior settings are detailed in the supplementary information.

In brief, the pseudotime and related topological parameters of the bifurcative trajectories in MGPfact are inferred by Gaussian process regression from downsampled single-cell transcriptomic data (MURP). Specifically, T is treated as a continuous variable representing the progression of cells through the differentiation process. We describe the relationship between pseudotime and expression data as:

where f(T) is a Gaussian Process (GP) with covariance matrix S, and ε represents the error term. The Gaussian process is defined as:

where  is the variance set to 1e-6. During inference, we update the pseudotime by maximizing the posterior liklihood. Specifically, the posterior distribution of pseudotime is obtained by combining the observed data Y* with the prior distribution of the Gaussian process model.

We use the Markov Chain Monte Carlo method for parameter estimation, particularly employing the adaptive Metropolis-within-Gibbs (AMWG) sampling to handle the high autocorrelation of pseudotime.

Comment#8: Enhancing Readability: For clarity, provide intuitive descriptions of each evaluation function used in simulated and real data. The novel methodology performs well for some metrics but less so for others. A clear understanding of these measurements is essential.

To address the concern of readability, we have added descriptions of 5 evaluation metrics in the methodology section (Benchmarking MGPfact to state-of-the-art methods) in line 494 to 515. Additionally, we have included a summary and discussion of these metrics in the conclusion section in line 214-240 to help the readers better understand the significance and impact of these measurements.

(1) In brief, the Hamming-Ipsen-Mikhailov (HIM) distance measures the similarity between topological structures, combining the normalized Hamming distance and the Ipsen-Mikhailov distance, which focus on edge length differences and degree distribution similarity, respectively. The F1_branches is used to assess the accuracy of a model's branch assignment via Jaccard similarity between branch pairs. In trajectory inference, cor_dist quantifies the similarity of inter-cell distances between predicted and true trajectories, evaluating the accuracy of cell ordering. The wcor_features assesses the similarity of key features through weighted Pearson correlation, capturing biological variation. The Overall score is calculated as the geometric mean of these metrics, providing an assessment of overall performance.

(2) For MGPfact and the other seven methods included in the comparison, each has its own focus. MGPfact specializes in factorizing complex cell trajectories using Gaussian process mixture models, making it particularly capable of identifying bifurcation events. Therefore, it excels in the accuracy of branch partitioning and similarity of trajectory topology. Among other methods, scShaper (Smolander et al., 2022) and TSCAN(Ji and Ji, 2016) are more suited for generating linear trajectories and excel in linear datasets, accurately predicting pseudotime. The Monocle series, as typical representatives of tree methods, effectively capture complex topologies and are suitable for analyzing cell data with diversified differentiation paths.

Comment#9: Microglia Analysis:In Figures 3A-C, the genes mentioned in the text for each bifurcation do not always match those shown in the panels. Please confirm this.

Thank you for pointing this out. We have carefully reviewed the article and corrected the error where the genes shown in the figures did not correspond to the descriptions in the article. The specific corrections have been made between line 257 and 264:

“The first bifurcation determines the differentiated cell fates of PAM and HM, which involves a set of notable marker genes of both cell types, such as Apoe, Selplg (HM), and Gpnmb (PAM). The second bifurcation determines the proliferative status, which is crucial for the development and function of PAM and HM (Guzmán, n.d.; Li et al., 2019). The genes affected by the second bifurcation are associated with cell cycle and proliferation, such as Mki67, Tubb5, Top2a. The third bifurcation influences the development and maturity of microglia, of which the highly weighted genes, such as Tmem119, P2ry12, and Sepp1 are all previously annotated markers for establishment of the fates of microglia (Anderson et al., 2022; Li et al., 2019) (Supplementary Table 4).”

Comment#10: Regulons:

- The conclusions rely heavily on regulons. The Methods section describes using SCENIC, GENIE3, RCisTarget, and AUCell, but their relation to bifurcation analysis is unclear.

- Do you perform trajectory analysis on all MURP-derived cells or within each identified trajectory based on bifurcation? This point needs clarification to make the outcomes comprehensible. The legend of Figure 4 provides some ideas, but further clarity is required.

Thank you for the comments.

(1) To clarify, we used the tools like SCENIC to annotate the highly weighted genes (HWG) resulted from the bifurcation analysis for transcription factor regulation activity and possible impacts on biological processes. We have added descriptions to the analysis of our microglial data. The revised content is between line 265 and 266:

“Moreover, we retrieved highly active regulons from the HWG by MGPfact, of which the significance is quantified by the overall weights of the member genes.”

(2) We apologize for any confusion caused by our description. It is important to clarify that we performed an overall trajectory analysis on all MURP results, rather than analyzing within each identified trajectory. Specifically, we first used MURP to downsample all preprocessed cells, where each MURP subset represents a group of cells. We then conducted trajectory inference on all MURP subsets and identified bifurcation points. This process generated multiple independent differentiation trajectories, encompassing all MURP subsets. To clearly convey this point, we have added descriptions in the legend of Figure 4. The revised content is between line 276 and 283:

“Fig. 4. MGPfact reconstructed the developmental trajectory of microglia, recovering known determinants of microglia fate. a-c. The inferred independent bifurcation processes with respect to the unique cell types (color-coded) of microglia development, where phase 0 corresponds to the state before bifurcation; and phases 1 and 2 correspond to the states post-bifurcation. Each colored dot represents a metacell of unique cell type defined by MURP. The most highly weighted regulons in each trajectory were labeled by the corresponding transcription factors (left panels). The HWG of each bifurcation process include a set of highly weighted genes (HWG), of which the expression levels differ significantly among phases 1, 2, and 3 (right panels).”

Comment#11: CD8+ T Cells: The comparison is made against Monocle2, the method used in the publication, but it would be beneficial to compare it with more recent methods. Otherwise, the added value of MGPfact is unclear.

Per your request, we have expanded our comparative analysis to include not only Monocle2 but also more recent methods such as Monocle3 (Cao et al., 2019) and scFates Tree (Faure et al., 2023). We used adjusted R-squared values to evaluate each method's ability to explain trajectory variation. The results have been added to Table 2 and Supplementary Table 6. The revised content is between line 318 and 326:

We assessed the goodness-of-fit (adjusted R-square) of the consensus trajectory derived by MGPfact and three methods (Monocle 2, Monocle 3 and scFates Tree) for the CD8+ T cell subtypes described in the original studies (Guo et al., 2018; Zhang et al., 2018). The data showed that MGPfact significantly improved the explanatory power for most CD8+ T cell subtypes over Monocle 2, which was used in the original studies (P < 0.05, see Table 2 and Supplementary Table 6), except for the CD8-GZMK cells in the CRC dataset. Additionally, MGPfact demonstrated better explanatory power in specific cell types when compared to Monocle 3 and scFates Tree. For instance, in the NSCLC dataset, MGPfact exhibited higher explanatory power for CD8-LEF1 cells (Table 2, R-squared = 0.935), while Monocle 3 and scFates Tree perform better in other cell types.

Comment#12: Consensus Trajectory: A panel explaining how the consensus trajectory is generated would be helpful. Include both visual and textual explanations tailored to the journal's audience.

Thank you for the comments. Regarding how the consensus trajectory is constructed, we have illustrated and described this in Figure 1 and the supplementary methods. Taking the reviewers' suggestions into account, we have added more details about the generation process of the consensus trajectory in the methods section to enhance the completeness of the manuscript. The revised content is from line 599 to 606:

“Following MGPfact decomposition, we obtained multiple independent bifurcative trajectories, each corresponds to a binary tree within the temporal domain. These trajectories were then merged to construct a coherent diffusion tree, representing the consensus trajectory of cells’ fate. The merging process involves initially sorting all trajectories by their bifurcation time. The first (earliest) bifurcative trajectory is chosen as the initial framework, and subsequent trajectories are integrated to the initial framework iteratively by adding the corresponding branches at the bifurcation timepoints. As a result, the trajectories are ultimately merged into a comprehensive binary tree, serving as the consensus trajectory.”

Comment#13: Discussion:

- Check for typos, e.g., line 382 "pseudtime.".

- Avoid considering HVG as the entire feature space.

- The first three paragraphs are too similar to the Introduction. Consider shortening them to succinctly state the scenario and the implications of your contribution.

Thank you for pointing out the typos.

(1) We conducted a comprehensive review of the document to ensure there are no typographical errors.

(2) We restructured the first three paragraphs of the discussion section to clarify the limitations in the use of current manifold-learning methods and removed any absolute language regarding treating HVGs as the entire feature space. The revised content is from line 419 to 430:

“Single-cell RNA sequencing (scRNA-seq) provides a direct, quantitative snapshot of a population of cells in certain biological conditions, thereby revealing the actual cell states and functions. Although existing clustering and embedding algorithms can effectively reveal discrete biological states of cells, these methods become less efficient when depicting continuous evolving of cells over the temporal domain. The introduction of manifold learning offers a new dimension for discovery of relevant biological knowledge in cell fate determination, allowing for a better representation of continuous changes in cells, especially in time-dependent processes such as development, differentiation, and clonal evolution. However, current manifold learning methods face major limitations, such as the need for prior information on pseudotime and cell clustering, and lack of explainability, which restricts their applicability. Additionally, many existing trajectory inference methods do not support gene selection, making it difficult to annotate the results to known biological entities, thereby hindering the interpretation of results and subsequent functional studies.”

Comment#14: Minor Comments:

(1) Review the paragraph regarding the "current manifold-learning methods are faced with two major challenges." The message needs clarification.

(2) Increase the quality of the figures.

(3) Update the numbering of equations from #(.x) to (x).

We thank the reviewer for these detailed suggestions.

(1) We have thoroughly revised the discussion section, addressing overly absolute statements. The revised content is from line 426 to 428:

“However, current manifold learning methods face major limitations, such as the need for prior information on pseudotime and cell clustering, and lack of explainability, which restricts their applicability.”

(2) We conducted a comprehensive review of the figures in the article to more clearly present our results.

(3) We have meticulously reviewed the equations in the article to ensure there are no display issues with the indices.

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Author response:

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

In summary, the changes made in the revision process include:

An addition of a paragraph in the result section that discusses the absolute values of measured Young’s moduli in the light of probing frequencies, accompanied by a new supplementary figure and a supplementary table that support that discussion

- Fig. S10. Absolute Young’s modulus values across the frequencies characteristic for the three measurement methods.

- Table S9. Operation parameters of the three methods used for characterizing the mechanical properties of cells.

Three new supplementary figures that display the expression matrices for the genes from the identified modules in carcinoma datasets used for validation:

- Fig. S4. Expression of identified target genes in the CCLE microarray dataset used for validation.

- Fig. S5. Expression of identified target genes in the CCLE RNA-Seq dataset used for validation.

- Fig. S6. Expression of identified target genes in the Genentech dataset used for validation.

An addition of a paragraph in the discussion section that discusses the intracellular origins of resistance to deformation and the dominance of actin cortex at low deformations.

- Refinement of the manuscript text and figures based on the specific feedback from the Reviewers.

Please see below for detailed responses to the Reviewers’ comments.

Reviewer #1 (Public Review)

In this work, Urbanska and colleagues use a machine-learning based crossing of mechanical characterisations of various cells in different states and their transcriptional profiles. Using this approach, they identify a core set of five genes that systematically vary together with the mechanical state of the cells, although not always in the same direction depending on the conditions. They show that the combined transcriptional changes in this gene set is strongly predictive of a change in the cell mechanical properties, in systems that were not used to identify the genes (a validation set). Finally, they experimentally after the expression level of one of these genes, CAV1, that codes for the caveolin 1 protein, and show that, in a variety of cellular systems and contexts, perturbations in the expression level of CAV1 also induce changes in cell mechanics, cells with lower CAV1 expression being generally softer. 

Overall the approach seems accessible, sound and is well described. My personal expertise is not suited to judge its validity, novelty or relevance, so I do not make comments on that. The results it provides seem to have been thoroughly tested by the authors (using different types of mechanical characterisations of the cells) and to be robust in their predictive value. The authors also show convincingly that one of the genes they identified, CAV1, is not only correlated with the mechanical properties of cells, but also that changing its expression level affects cell mechanics. At this stage, the study appears mostly focused on the description and validation of the methodological approach, and it is hard to really understand what the results obtain really mean, the importance of the biological finding - what is this set of 5 genes doing in the context of cell mechanics? Is it really central, or is it just one of the set of knobs on which the cell plays - and it is identified by this method because it is systematically modulated but maybe, for any given context, it is not the dominant player - all these fundamental questions remain unanswered at this stage. On one hand, it means that the study might have identified an important novel module of genes in cell mechanics, but on the other hand, it also reveals that it is not yet easy to interpret the results provided by this type of novel approach. 

We thank the Reviewer #1 for the thoughtful evaluation of our manuscript. The primary goal of the manuscript was to present a demonstration of an unbiased approach for the identification of genes involved in the regulations of cell mechanics. The manuscript further provides a comprehensive computational validation of all genes from the identified network, and experimental validation of a selected gene, CAV1. 

We agree that at the current stage, far-reaching conclusions about the biological meaning of the identified network cannot be made. We are, however, convinced that the identification of an apparently central player such as CAV1 across various cellular systems is per se meaningful, in particular since CAV1 modulation shows clear effects on the cell mechanical state in several cell types. 

We anticipate that our findings will encourage more mechanistic studies in the future, investigating how these identified genes regulate mechanical properties and interact with each other. Notwithstanding, the identified genes (after testing in specific system of interest) can be readily used as genetic targets for modulating mechanical properties of cells. Access to such modifications is of huge relevance not only for performing further research on the functional consequence of cell mechanics changes (in particular in in-vivo systems where using chemical perturbations is not always possible), but also for the potential future implementation in modulating mechanical properties of the cells to prevent disease (for example to inhibit cancer metastasis or increase efficacy of cancer cell killing by cytotoxic T cells).

We have now added a following sentence in the first paragraph of discussion to acknowledge the open ends of our study:

“(...). Here we leveraged this opportunity by performing discriminative network analysis on transcriptomes associated with mechanical phenotype changes to elucidate a conserved module of five genes potentially involved in cell mechanical phenotype regulation. We provided evidence that the inferred conserved functional network module contains an ensemble of five genes that, in particular when combined in a unique combinatorial marker, are universal, specific and trustworthy markers of mechanical phenotype across the studied mouse and human systems. We further demonstrated on the example of a selected marker gene, CAV1, that its experimental up- and downregulation impacts the stiffness of the measured cells. This demonstrates that the level of CAV1 not only correlates with, but also is causative of mechanical phenotype change. The mechanistic insights into how precisely the identified genes are involved in regulating mechanical properties, how they interact with each other, and whether they are universal and dominant in various contexts all remain to be established in

future studies.”

Reviewer #2 (Public Review)

A key strength is the quantitative approaches all add rigor to what is being attempted. The approach with very different cell culture lines will in principle help identify constitutive genes that vary in a particular and predictable way. To my knowledge, one other study that should be cited posed a similar pan-tissue question using mass spectrometry proteomics instead of gene expression, and also identified a caveolae component (cavin-1, PTRF) that exhibited a trend with stiffness across all sampled tissues. The study focused instead on a nuclear lamina protein that was also perturbed in vitro and shown to follow the expected mechanical trend (Swift et al 2013). 

We thank the Reviewer #2 for the positive evaluation of the breadth of the results and for pointing us to the relevant reference for the proteomic analysis related to tissue stiffness (Swift et al., 2013). This study, which focused primarily on the tissue-level mechanical properties, identifying PTRF, a caveolar component, which links to our observation of another caveolar component, CAV1, at the single-cell level. 

We have now included the citation in the following paragraph of the discussion:

“To our knowledge, there are no prior studies that aim at identifying gene signatures associated with single-cell mechanical phenotype changes, in particular across different cell types. There are, however, several studies that investigated changes in expression upon exposure of specific cell types to mechanical stimuli such as compression (87, 88) or mechanical stretch (22, 80, 89), and one study that investigated difference in expression profiles between stiffer and softer cells sorted from the same population (90). Even though the studies concerned with response to mechanical stimuli answer a fundamentally different question (how gene expression changes upon exposure to external forces vs which genes are expressed in cells of different mechanical phenotype), we did observe some similarities in the identified genes. For example, in the differentially expressed genes identified in the lung epithelia exposed to compression (87), three genes from our module overlapped with the immediate response (CAV1, FHL2, TGLN) and four with the long-term one (CAV1, FHL2, TGLN, THBS1). We speculate that this substantial overlap is caused by the cells undergoing change in their stiffness during the response to compression (and concomitant unjamming transition). Another previous study explored the association between the stiffness of various tissues and their proteomes. Despite the focus on the tissue-scale rather than single-cell elasticity, the authors identified polymerase I and transcript release factor (PTRF, also known as cavin 1 and encoding for a structural component of the caveolae) as one of the proteins that scaled with tissue stiffness across samples (91).”

Reviewer #3 (Public Review)

In this work, Urbanska et al. link the mechanical phenotypes of human glioblastoma cell lines and murine iPSCs to their transcriptome, and using machine learning-based network analysis identify genes with putative roles in cell mechanics regulation. The authors identify 5 target genes whose transcription creates a combinatorial marker which can predict cell stiffness in human carcinoma and breast epithelium cell lines as well as in developing mouse neurons. For one of the target genes, caveolin1 (CAV1), the authors perform knockout, knockdown, overexpression and rescue experiments in human carcinoma and breast epithelium cell lines. They determine the cell stiffness via RT-DC, AFM indentation and AFM rheology and confirm that high CAV1 expression levels correlate with increased stiffness in those model systems. This work brings forward an interesting approach to identify novel genes in an unbiased manner, but surprisingly the authors validate caveolin 1, a target gene with known roles in cell mechanics regulation. 

I have two main concerns with the current version of this work: 

(1) The authors identify a network of 5 genes that can predict mechanics. What is the relationship between the 5 genes? If the authors aim to highlight the power of their approach by knockdown, knockout or over-expression of a single gene why choose CAV1 (which has an individual p-value of 0.16 in Fig S4)? To justify their choice, the authors claim that there is limited data supporting the direct impact of CAV1 on mechanical properties of cells but several studies have previously shown its role in for example zebrafish heart stiffness, where a knockout leads to higher stiffness (Grivas et al., Scientific Reports 2020), in cancer cells, where a knockdown leads to cell softening (Lin et al., Oncotarget 2015), or in endothelial cell, where a knockout leads to cell softening (Le Master et al., Scientific Reports 2022). 

We thank the reviewer for their comments. First, we do acknowledge that studying the relationship between the five identified genes is an intriguing question and would be a natural extension of the currently presented work. It is, however, beyond the scope of presented manuscript, in which our primarily goal was to introduce a general pipeline for de novo identification of genes related to cell mechanics. We did add a following statement in the discussion (yellow highlight) to acknowledge the open ends of our study:

“The mechanical phenotype of cells is recognized as a hallmark of many physiological and pathological processes. Understanding how to control it is a necessary next step that will facilitate exploring the impact of cell mechanics perturbations on cell and tissue function (76).

The increasing availability of transcriptional profiles accompanying cell state changes has recently been complemented by the ease of screening for mechanical phenotypes of cells thanks to the advent of high-throughput microfluidic methods (77). This provides an opportunity for data-driven identification of genes associated with the mechanical cell phenotype change in a hypothesis-free manner. Here we leveraged this opportunity by performing discriminative network analysis on transcriptomes associated with mechanical phenotype changes to elucidate a conserved module of five genes potentially involved in cell mechanical phenotype regulation. We provided evidence that the inferred conserved functional network module contains an ensemble of five genes that, in particular when combined in a unique combinatorial marker, are universal, specific and trustworthy markers of mechanical phenotype across the studied mouse and human systems. We further demonstrated on the example of a selected marker gene, CAV1, that its experimental up- and downregulation impacts the stiffness of the measured cells. This demonstrates that the level of CAV1 not only correlates with, but also is causative of mechanical phenotype change. The mechanistic insights into how precisely the identified genes are involved in regulating mechanical properties, how they interact with each other, and whether they are universal and dominant in various contexts all remain to be established in future studies.”

Regarding the selection of CAV1 as the gene that we used for validation experiment; as mentioned in the introductory paragraph of the result section “Perturbing expression levels of CAV1 changes cells stiffness” (copied below), we were encouraged by the previous data already linking CAV1 with cell mechanics when selecting it as our first target. The relationship between CAV1 and cell mechanics regulation, however, is not very well established (of note, two of the latest manuscripts came out after the initial findings of our study). 

Regarding the citations suggested by the reviewer: two are already included in the original manuscript (Lin et al., Oncotarget 2015 – Ref (63), Le Master –2022 Ref (67)), along with an additional one (Hsu et al 2018 (66)), and the third one (Grivas et al, 2020 (68)) is now also added to the manuscript. Though, we would like to highlight that even though Grivas et al state that the CAV1 KO cells are stiffer, the AFM indentation measurements were performed on the cardiac tissue, with a spherical tip of 30 μm radius and likely reflect primarily supracelluar, tissue-scale properties, as opposed to cell-scale measurements performed in our study (we used cultured cells which mostly lack the extracellular tissue structures, deformability cytometry was performed on dissociated cells and picks up on cell properties exclusively, and in case of AFM measurements a spherical tip with 5 μm radius was used).

“We decided to focus our attention on CAV1 as a potential target for modulating mechanical properties of cells, as it has previously been linked to processes intertwined with cell mechanics. In the context of mechanosensing, CAV1 is known to facilitate buffering of the membrane tension (45), play a role in β1-inegrin-dependent mechanotransduction (58) and modulate the mechanotransduction in response to substrate stiffness (59). CAV1 is also intimately linked with actin cytoskeleton — it was shown to be involved in cross-talk with Rho-signaling and actin cytoskeleton regulation (46, 60–62), filamin A-mediated interactions with actin filaments (63), and co-localization with peripheral actin (64). The evidence directly relating CAV1 levels with the mechanical properties of cells (47, 62, 65, 66) and tissues (66, 67) , is only beginning to emerge.”

Regarding the cited p-value of 0.16, we would like to clarify that it is the p-value associated with the coefficient of the crude linear regression model fitted to the data for illustrative purposes in Fig S4. This value only says that from the linear fit we cannot conclude much about the correlation of the level of Cav1 with the Young’s modulus change. Much more relevant parameters to look at are the AUC-ROC values and associated p-values reported in the Table 4 in the main text (see below), which show good performance of CAV1 in separating soft and stiff cell states. 

The positive hypothesis I assumes that markers are discriminative of samples with stiff/soft mechanical phenotype regardless of the studied biological system, and CAV1 has a clear trend with the minimum AUC-ROC on 3 datasets of 0.78, even though the p-value is below the significance level. The positive hypothesis II assumes that markers are discriminative of samples with stiff/soft mechanical phenotype in carcinoma regardless of data source, and CAV1 has a clear significance because the minimum AUC-ROC on 3 datasets is 0.89 and the p-value is 0.02.

(2) The authors do not show how much does PC-Corr outperforms classical co-expression network analysis or an alternative gold standard. It is worth noting that PC-Corr was previously published by the same authors to infer phenotype-associated functional network modules from omics datasets (Ciucci et al., Scientific Reports 2017). 

As pointed out by the Reviewer, PC-corr has been introduced and characterized in detail in a previous publication (Ciucci et al, 2017, Sci. Rep.), where it was compared against standard co-expression analysis (below reported as: p-value network) on molecules selected using univariate statistical analysis. 

See the following fragment of Discussion in Ciucci et al, 2017:

“The PC-corr networks were always compared to P-value networks. The first strategical difference lies in the way features are selected: while the PC-corr adopts a multivariate approach, i.e. it uses a combination of features that are responsible for the sample discrimination, in the P-value network the discriminating features are singly selected (one by one) with each Mann-Whitney test (followed by Benjamini-Hochberg procedure). The second strategical difference lies in the generation of the correlation weights in the network. PC-corr combines in parallel and at the same time in a unique formula the discrimination power of the PC-loadings and the association power of the Pearson correlation, directly providing in output discriminative omic associations. These are generated using a robust (because we use as merging factor the minimum operator, which is a very penalizing operator) mathematical trade-off between two important factors: multivariate discriminative significance and correlation association. In addition, as mentioned above, the minimum operator works as an AND logical gate in a digital circuit, therefore in order to have a high link weight in the PCcorr network, both the discrimination (the PC-loadings) and the association (the Pearson correlations) of the nodes adjacent to the link should be simultaneously high. Instead, the Pvalue procedure begins with the pre-selection of the significant omic features and, only in a second separated step, computes the associations between these features. Therefore, in P-value networks, the interaction weights are the result neither of multivariate discriminative significance, nor of a discrimination/association interplay.”

Here we implement PC-corr for a particular application and do not see it as central to the message of the present manuscript to compare it with other available methods. We considered it much more relevant to focus on an in-silico validation on dataset not used during the PCcorr analysis (see Table 3 and 4 for details).

Altogether, the authors provide an interesting approach to identify novel genes associated with cell mechanics changes, but the current version does not fulfill such potential by focusing on a single gene with known roles in cell mechanics. 

Our manuscript presents a demonstration of an overall approach for the identification of genes involved in the regulation of cell mechanics, and the perturbations performed on CAV1 have a demonstrative role (please also refer to the explanations of why we decided to perform the verification focused on CAV1 above). The fact that we identify CAV1, which has been implicated in regulating cell mechanics in a handful of studies, de novo and in an unbiased way speaks to the power of our approach. We do agree that investigation into the effect of manipulating the expression of the remaining genes from the identified network module, as well as into the mutual relationships between those genes and their covariance in perturbation experiments, constitutes a desirable follow-up on the presented results. It is, however, beyond the scope of the current manuscript. Regardless, the other genes identified can be readily tested in systems of interest and used as potential knobs for tuning mechanical properties on demand.

Reviewer #1 (Recommendations For Authors)

I am not a specialist of the bio-informatics methods used in this study, so I will not make any specific technical comments on them. 

In terms of mechanical characterisation of cells, the authors use well established methods and the fact that they systematically validate their findings with at least two independent methods (RT-DC and AFM for example) makes them very robust. So I have no concerns with this part.  The experiments of perturbations of CAV 1 are also performed to the best standards and the results are clear, no concern on that. 

My main concerns are rather questions I was asking myself and could not answer when reading the article. Maybe the authors could find ways to clarify them - the discussion of their article is already very long and maybe it should not be lengthened to much. In my opinion, some of the points discussed are not really essential and rather redundant with other parts of the paper. This could be improved to give some space to clarify some of the points below:  

We thank the Reviewer #1 for an overall positive evaluation of the manuscript as well as the points of criticism which we addressed in a point-by-point manner below.

(1) This might be a misunderstanding of the method on my side, but I was wondering whether it is possible to proceed through the same steps but choose other pairs of training datasets amongst the 5 systems available (there are 10 such pairs if I am not mistaken) and ask whether they always give the same set of 5 genes. And if not, are the other sets also then predictive, robust, etc. Or is it that there are 'better' pairs than others in this respect. Or the set of 5 genes is the only one that could be found amongst these 5 datasets - and then could it imply that it is the only group 'universal' group of predictive genes for cell mechanics (when applied to any other dataset comprising similar mechanical measures and expression profiles, for other cells, other conditions)? 

I apologize in case this question is just the result of a basic misunderstanding of the method on my side. But I could not answer the question myself based on what is in the article and it seems to be important to understand the significance of the finding and the robustness of the method. 

We thank the Reviewer for this question. To clarify: while in general it is possible to proceed through the same analysis steps choosing a different pair of datasets (see below for examples), we have purposefully chosen those two and not any other datasets because they encompassed the highest number of samples per condition in the RNAseq data (see Fig 4 and Table R1 below), originated from two different species and concerned least related tissues (the other option for mouse would be neural progenitors which in combination with the glioblastoma would likely result in focusing on genes expressed in neural tissues). This is briefly explained in the following fragment of the manuscript on Page 10:

“For the network construction, we chose two datasets that originate from different species, concern unrelated biological processes, and have a high number of samples included in the transcriptional analysis: human glioblastoma and murine iPSCs (Table 1).”

To further address the comment of the reviewer: there is indeed a total of 10 possible two-set combinations of datasets, 6 of those pairs are human-mouse combinations (highlighted in orange in Author response Table 1), 3 are human-human combinations (highlighted in blue), and 1 is mousemouse (marked in green).

Author response table 1.

Possible two-set combinations of datasets. For each combination, the number of common genes is indicated. The number on the diagonal represents total number of transcripts in the individual datasets, n corresponds to the number of samples in the respective datasets.  * include non-coding genes.

To reiterate, we have chosen the combination of set A (glioblastoma) and set D (iPSCs) to choose datasets from different species and with highest sample number. 

As for the other combinations of human-mouse datasets:

• set A & E lead to derivation of a conserved module, however as expected this module includes genes specific for neuronal tissues (such as brain & testis specific immunoglobulin IGSF11, or genes involved in neuronal development such as RFX4, SOX8)

Author response image 1.

• the remaining combinations (set B&D, B&E, C&D and C&E) do not lead to a derivation of a highly interconnected module

Author response image 2.

Author response image 3.

Author response image 4.

Author response image 5.

Finally, it would have also been possible to perform the combined PC-corr procedure on all 5 datasets. However, this would prevent us from doing validation using unknown datasets.

Hence, we decided to proceed with the 2 discovery and 4 validation datasets.

For the sake of completeness, we present below some of the networks obtained from the analysis performed on all 5 datasets (which intersect at 8059 genes).

Author response image 6.

The above network was created by calculating mean/minimum PC-corr among all five datasets and applying the threshold. The thresholding can be additionally restricted in that we:

a. constrain the directionality of the correlation between the genes (𝑠𝑔𝑛(𝑐) ) to be the same among all or at least n datasets

b. constrain the directionality of the correlation between the cell stiffness and gene expression level (𝑠𝑔𝑛(𝑉)) for individual genes.

Some of the resulting networks for such restrictions are presented below.

Author response image 7.

Author response image 8.

Of note, some of the nodes from the original network presented in the paper (CAV1, FHL2, and IGFBP7) are preserved in the 5-set network (and highlighted with blue rims),

(2) The authors already use several types of mechanical characterisation of the cells, but there are even more of them, in particular, some that might not directly correspond to global cell stiffness but to other aspects, like traction forces, or cell cortex rheology, or cell volume or passage time trough constrictions (active or passive) - they might all be in a way or another related, but they are a priori independent measures. Would the authors anticipate finding very different 'universal modules' for these other mechanical properties, or again the same one? Is there a way to get at least a hint based on some published characterisations for the cells used in the study? Basically, the question is whether the gene set identified is specific for a precise type of mechanical property of the cell, or is more generally related to cell mechanics modulation - maybe, as suggested by the authors because it is a set of molecular knobs acting upstream of general mechanics effectors like YAP/TAZ or acto-myosin? 

We thank the Reviewer for this comment. We would like to first note that in our study, we focused on single-cell mechanical phenotype understood as a response of the cells to deformation at a global (RT-DC) or semi-local (AFM indentation with 5-μm bead) level and comparatively low deformations (1-3 μm, see Table S9). There is of course a variety of other methods for measuring cell mechanics and mechanics-related features, such as traction force microscopy mentioned by the reviewer. Though, traction force microscopy probes how the cells apply forces and interact with their environment rather than the inherent mechanical properties of the cells themselves which were the main interest of our study. 

Nevertheless, as mentioned in the discussion, we found some overlap with the genes identified in other mechanical contexts, for example in the context of mechanical stretching of cells:

“Furthermore, CAV1 is known to modulate the activation of transcriptional cofactor yesassociated protein, YAP, in response to changes in stiffness of cell substrate (60) and in the mechanical stretch-induced mesothelial to mesenchymal transition (74).”

Which suggests that the genes identified here may be more broadly related to mechanical aspects of cells. 

Of note, we do have some insights connected to the changes of cell volume — one of the biophysical properties mentioned by the reviewer — from our experiments.  For all measurements performed with RT-DC, we can also calculate cell volumes from 2D cell contours (see Author response images 9, 10, and 11). For most of the cases (all apart from MEF CAV1KO), the stiffer phenotype of the cells, associated with higher levels of CAV1, shows a higher volume.

Author response image 9.

Cell volumes for the divergent cell states in the five characterized biological systems. (A) Glioblastoma. (B) Carcinoma, (C) MCF10A, (D) iPSCs, (E) Developing neurons. Data corresponds to Figure 2. Cell volumes were estimated using Shape-Out 1.0.10 by rotation of the cell contours.

Author response image 10.

Cell volumes for CAV1 perturbation experiments. (A) CAV1 knock down performed in TGBC cells. (B) CAV1 overexpression in ECC4 and TGBC cells. Data corresponds to Figure 5. Cell volumes were estimated using Shape-Out 1.0.10 by rotation of the cell contours.  

Author response image 11.

Cell volumes for WT and CAV1KO MEFs. Data corresponds to Figure S9. Cell volumes were estimated using Shape-Out 1.0.10 by rotation of the cell contours.  

(3) The authors have already tested a large number of conditions in which perturbations of the level of expression of CAV1 correlates with changes in cell mechanics, but I was wondering whether it also has some direct explanatory value for the initial datasets used - for example for the glioblastoma cells from Figure 2, in the different media, would a knock-down of CAV1 prevent the increase in stiffness observed upon addition of serum, or for the carcinoma cells from different tissues treated with different compounds - if I understand well, the authors have tested a subset of these (ECC4 versus TGBC in figure 5) - how did they choose these and how general is it that the mechanical phenotype changes reported in Figure 2 are all mostly dependant on CAV1 expression level? I must say that the way the text is written and the results shown, it is hard to tell whether CAV1 is really having a dominant effect on cell mechanics in most of these contexts or only a partial effect. I hope I am being clear in my question - I am not questioning the conclusions of Figures 5 and 6, but asking whether the level of expression of CAV1, in the datasets reported in Figure 2, is the dominant explanatory feature for the differences in cell mechanics. 

We thank reviewer for this comment and appreciate the value of the question about the generality and dominance of CAV1 in influencing cell mechanics.

On the computational side, we have addressed these issues by looking at the performance of CAV1 (among other identified genes) in classifying soft and stiff phenotypes across biological systems (positive hypothesis I), as well as across data of different type (sequencing vs microarray data) and origin (different research institutions) (positive hypothesis II). CAV1 showed strong classification performance (Table 4), suggesting it is a general marker of stiffness changes.  

On the experimental side, we conducted the perturbation experiments in two systems of choice: two intestinal carcinoma cell lines (ECC4 and TGBC) and the MCF10A breast epithelial cell line. These choices were driven by ease of handling, accessibility, as well as (for MCF10A) connection with a former study (Taveres et al, 2017). While we observed correlations between CAV1 expression and cell mechanics in wide range of datasets, the precise role of CAV1 in each system may vary, and further perturbation experiments in specific systems could be performed to solidify the direct/dominant role of CAV1 in cell mechanics. We hypothesize that the suggested knockdown of CAV1 upon serum addition in glioblastoma cells could reduce or prevent the increase in stiffness observed, though this experiment has not been performed. 

In conclusion, while the computational analysis gives us confidence that CAV1 is a good indicator of cell stiffness, we predict that it acts in concert with other genes and in specific context could be replaced by other changes. We suggest that the suitability of CAV1 for manipulation of the mechanical properties should be tested in each system of interested before use. 

To highlight the fact that the relevance of CAV1 for modulating cell mechanics in specific systems of interest should be tested and the mechanistic insights into how CAV1 regulates cell mechanics are still missing, we have added the following sentence in the discussion:

“The mechanical phenotype of cells is recognized as a hallmark of many physiological and pathological processes. Understanding how to control it is a necessary next step that will facilitate exploring the impact of cell mechanics perturbations on cell and tissue function (76). The increasing availability of transcriptional profiles accompanying cell state changes has recently been complemented by the ease of screening for mechanical phenotypes of cells thanks to the advent of high-throughput microfluidic methods (77). This provides an opportunity for data-driven identification of genes associated with the mechanical cell phenotype change in a hypothesis-free manner. Here we leveraged this opportunity by performing discriminative network analysis on transcriptomes associated with mechanical phenotype changes to elucidate a conserved module of five genes potentially involved in cell mechanical phenotype regulation. We provided evidence that the inferred conserved functional network module contains an ensemble of five genes that, in particular when combined in a unique combinatorial marker, are universal, specific and trustworthy markers of mechanical phenotype across the studied mouse and human systems. We further demonstrated on the example of a selected marker gene, CAV1, that its experimental up- and downregulation impacts the stiffness of the measured cells. This demonstrates that the level of CAV1 not only correlates with, but also is causative of mechanical phenotype change. The mechanistic insights into how precisely the identified genes are involved in regulating mechanical properties, how they interact with each other, and whether they are universal and dominant in various contexts all remain to be established in future studies.”

(4) It would be nice that the authors try to more directly address, in their discussion, what is the biological meaning of the set of 5 genes that they found - is it really mostly a product of the methodology used, useful but with little specific relevance to any biology, or does it have a deeper meaning? Either at a system level, or at an evolutionary level. 

We would like to highlight that our manuscript is focused on the method that we introduce to identify sets of genes involved in the regulation of cell mechanics. The first implementation included here is only the beginning of this line of work which, in the future, will include looking in detail at the biological meaning and the interconnectivity of the genes identified. Most likely, there is a deeper meaning of the identified module which could be revealed with a lot of dedicated future work. As it is a mere speculation at this point, we would like to refrain from going into more detail about it in the current manuscript. We provide below a few words of extended explanation and additional analysis that can shed light on the current limited knowledge of the connections between the genes and evolutionary preservation of the genes. 

While it is difficult to prove at present, we do believe that the identified node of genes may have an actual biological meaning and is not a mere product of the used methodology. The PC-corr score used for applying the threshold and obtaining the gene network is high only if the Pearson’s correlation between the two genes is high, meaning that the high connected module of genes identified show corelated expression and is likely co-regulated. Additionally, we performed the GO Term analysis using DAVID to assess the connections between the genes (Figure S3). We have now performed an additional analysis using two orthogonal tools the functional protein association tool STRING and KEGG Mapper. 

With STRING, we found a moderate connectivity using the five network nodes identified in our study, and many of the obtained connections were based on text mining and co-expression, rather than direct experimental evidence (Author response image 12A). A more connected network can be obtained by allowing STRING to introduce further nodes (Author response image 12B). Interestingly, some of the nodes included by STRING in the extended network are nodes identified with milder PCcorr thresholds in our study (such as CNN2 or IGFBP3, see Table S3). 

With KEGG Mapper, we did not find an obvious pathway-based clustering of the genes from the module either. A maximum of two genes were assigned to one pathway and those included: 

• focal adhesions (pathway hsa04510): CAV1 and THBS1

• cytoskeleton in muscle cells (pathway hsa04820): FHL2 and THBS1

• proteoglycans in cancer (pathway hsa05205): CAV1 and THBS1.

As for the BRITE hierarchy, following classification was found:

• membrane trafficking(hsa04131): CAV1, IGFBP7, TAGLN, THBS, with following subcategories:

- endocytosis / lipid raft mediated endocytosis/caveolin-mediated endocytosis:

CAV1

- endocytosis / phagocytosis / opsonins: THBS1

- endocytosis / others/ insulin-like growth factor-binding proteins: IGFBP7 o others / actin-binding proteins/others: TAGLN.

Taken together, all that analyses (DAVID, STRING, KEGG) show that at present no direct relationship/single pathway can be found that integrates all the genes from the identified modules. Future experiments, including investigations of how other module nodes are affected when one of the genes is manipulated, will help to establish actual physical or regulatory interactions between the genes from our module. 

To touch upon the evolutionary perspective, we provide an overview of occurrence of the genes from the identified module across the evolutionary tree. This overview shows that the five identified genes are preserved in phylum Chordata with quite high sequence similarity, and even more so within mammals (Author response image 13).

Author response image 12.

Visualisation of interactions between the nodes in the identified module using functional protein association networks tool STRING. (A) Connections obtained using multiple proteins search and entering the five network nodes. (B) Extended network that includes further genes to increase indirect connectivity. The genes are added automatically by STRING. Online version of STRING v12.0 was used with Homo sapiens as species of interest.   

Author response image 13.

Co-occurrence of genes from the network module across the evolutionary tree. Mammals are indicated with the green frame, glires (include mouse), as well as primates (include human) are indicated with yellow frames. The view was generated using online version of STRING 12.0.

Reviewer #2 (Recommendations For Authors) 

(1) The authors need to discuss the level of sensitivity of their mechanical measurements with RT-DC for changes to the membrane compared to changes in microtubules, nucleus, etc. The limited AFM measurements also seem membrane/cortex focused. For these and further reasons below, "universal" doesn't seem appropriate in the title or abstract, and should be deleted. 

We thank the reviewer for this comment. Indeed, RT-DC is a technique that deforms the entire cell to a relatively low degree (inducing ca 17% mean strain, i.e. a deformation of approximately 2.5 µm on a cell with a 15 µm diameter, see Table S9 and Urbanska et al., Nat Methods 2020). Similarly, the AFM indentation experiments performed in this study (using a 5-µm diameter colloidal probe and 1 µm indentation) induce low strains, at which, according to current knowledge, the actin cortex dominates the measured deformations. However, other cellular components, including the membrane, microtubules, intermediate filaments, nucleus, other organelles, and cytoplasmic packing, can also contribute. We have reviewed these contributions in detail in a recent publication (Urbanska and Guck, 2024, Ann Rev Biophys., PMID 38382116). For a particular system, it is hard to speculate without further investigation which parts of the cell have a dominant effect on the measured deformability. We have added now a following paragraph in the discussion to include this information:

“The mechanical phenotype of single cells is a global readout of cell’s resistance to deformation that integrates contributions from all cellular components. The two techniques implemented for measuring cell mechanical in this study — RT-DC and AFM indentation using a spherical indenter with 5 µm radius — exert comparatively low strain on cells (< 3 µm, see Table S9), at which the actin cortex is believed to dominate the measured response. However, other cellular components, including the membrane, microtubules, intermediate filaments, nucleus, other organelles, and cytoplasmic packing, also contribute to the measured deformations (reviewed in detail in (79)) and, for a particular system, it is hard to speculate without further investigation which parts of the cell have a dominant effect on the measured deformability.”

The key strength of measuring the global mechanics is that such measurements are agnostic of the specific origin of the resistance to shape change. As such, the term “universal” could be seen as rather appropriate, as we are not testing specific contributions to cell mechanics, and we see the two methods used (RT-DC and AFM indentation) as representative when it comes to measuring global cell mechanics. And we highlighted many times throughout the text that we are measuring global single-cell mechanical phenotype. 

Most importantly, however, we have used the term “universal” to capture that the genes are preserved across different systems and species, not in relation to the type of mechanical measurements performed and as such we would like to retain the term in the title.

(2) Fig.2 cartoons of tissues is a good idea to quickly illustrate the range of cell culture lines studied. However, it obligates the authors to examine the relevant primary cell types in singlecell RNAseq of human and/or mouse tissues (e.g. Tabula Muris). They need to show CAV1 is expressed in glioblastoma, iPSCs, etc and not a cell culture artifact. CAV1 and the other genes also need to be plotted with literature values of tissue stiffness.  

We thank the reviewer for this the comment; however, we do believe that the cartoons in Figure 2 should assist the reader to readily understand whether cultured cells derived from the respective tissues were used (see cartoons representing dishes), or the cells directly isolated from the tissue were measured (this is the case for the developing neurons dataset). 

We did, however, follow the suggestion of the reviewer to use available resources and checked the expression of genes from the identified network module across various tissues in mouse and human. We first used the Mouse Genome Informatics (MGI; https://www.informatics.jax.org/) to visualize the expression of the genes across organs and organ systems (Author response image 14) as well as across more specific tissue structures (Author response image 15). These two figures show that the five identified genes are expressed quite broadly in mouse. We next looked at the expression of the five genes in the scRNASeq dataset from Tabula Muris (Author response image 16). Here, the expression of respective genes seemed more restricted to specific cell clusters. Finally, we also collected the cross-tissue expression of the genes from our module in human tissues from Human Protein Atlas v23 at both mRNA (Author response image 17) and protein (Author response image 18) levels. CAV1, IGFBP7, and THBS1 showed low tissue specificity at mRNA level, FHL2 was enriched in heart muscle and ovary (the heart enrichment is also visible in Author response image 15 for mouse) and TAGLN in endometrium and intestine. Interestingly, the expression at the protein level (Author response image 18) did not seem to follow faithfully the mRNA levels (Author response image 17). Overall, we conclude that the identified genes are expressed quite broadly across mouse and human tissues. 

Author response image 14.

Expression of genes from the identified module across various organ and organ systems in mouse. The expression matrices for organs (A) and organ systems (B) were generated using Tissue x Gene Matrix tool of Gene eXpression Database (https://www.informatics.jax.org/gxd/, accessed on 22nd September 2024). No pre-selection of stage (age) and assay type (includes RNA and protein-based assays) was applied. The colors in the grid (blues for expression detected and reds for expression not detected) get progressively darker when there are more supporting annotations. The darker colors do not denote higher or lower levels of expression, just more evidence.

Author response image 15.

Expression of genes from the identified module across various mouse tissue structures. The expression matrices for age-selected mouse marked as adult (A) or young individuals (collected ages labelled P42-84 / P w6-w12 / P m1.5-3.0) (B) are presented and were generated using RNASeq Heatmap tool of Gene eXpression Database (https://www.informatics.jax.org/gxd/, accessed on 2nd October 2024).

Author response image 16.

Expression of genes from the identified module across various cell types and organs in t-SNE embedding of Tabula Muris dataset. (A) t-SNE clustering color-coded by organ. (B-F) t-SNE clustering colorcoded for expression of CAV1 (B), IGFBP7 (C), FHL2 (D), TAGLN (E), and THBS1 (F). The plots were generated using FACS-collected cells data through the visualisation tool available at https://tabulamuris.sf.czbiohub.org/ (accessed on 22nd September 2024).

Author response image 17.

Expression of genes from the identified module at the mRNA level across various human tissues. (A-E) Expression levels of CAV1 (A), IGFBP7 (B), FHL2 (C), TAGLN (D), and THBS1 (E). The plots were generated using consensus dataset from Human Protein Atlas v23 https://www.proteinatlas.org/ (accessed on 22nd September 2024).

Author response image 18.

Protein levels of genes from the identified module across various human tissues. (A-E) Protein levels of CAV1 (A), IGFBP7 (B), FHL2 (C), TAGLN (D), and THBS1 (E). The plots were generated using Human Protein Atlas v23 https://www.proteinatlas.org/ (accessed on 22nd September 2024).

Regarding literature values and tissue stiffness, we would like to argue that cell stiffness is not equivalent to tissue stiffness, and we are interested in the former. Tissue stiffness is governed by a combination of cell mechanical properties, cell adhesions, packing and the extracellular matrix. There can be, in fact, mechanically distinct cell types (for example characterized by different metabolic state, malignancy level etc) within one tissue of given stiffness. Hence, we consider that testing for the correlation between tissue stiffness and expression of identified genes is not immediately relevant.

(3) Fig.5D,H show important time-dependent mechanics that need to be used to provide explanations of the differences in RT-DC (5B,F) and in standard AFM indentation expts (5C,G). In particular, it looks to me that RT-DC is a high-f/short-time measurement compared to the AFM indentation, and an additional Main or Supp Fig needs to somehow combine all of this data to clarify this issue. 

We thank the reviewer for this comment. It is indeed the case, that cells typically display higher stiffness when probed at higher rates. We have now expanded on this aspect of the results and added a supplementary figure (Fig. S10) that illustrates the frequencies used in different methods and summarizes the apparent Young’s moduli values into one plot in a frequencyordered manner. Of note, we typically acquire RT-DC measurements at up to three flowrates, and the increase in measurement flow rates accompanying increase in flow rate also results in higher extracted apparent Young’s moduli (see Fig. S10 B,D). We have further added Table S9 that summarizes operating parameters of all three methods used for probing cell mechanics in this manuscript:

“The three techniques for characterizing mechanical properties of cells — RT-DC, AFM indentation and AFM microrheology — differ in several aspects (summarized in Table S9), most notably in the frequency at which the force is applied to cells during the measurements, with RT-DC operating at the highest frequency (~600 Hz), AFM microrheology at a range of frequencies in-between (3–200 Hz), and AFM indentation operating at lowest frequency (5 Hz) (see Table S9 and Figure S10A). Even though the apparent Young’s moduli obtained for TGBCS cells were consistently higher than those for ECC4 cells across all three methods, the absolute values measured for a given cell line varied depending on the methods: RT-DC measurements yielded higher apparent Young’s moduli compared to AFM indentation, while the apparent Young’s moduli derived from AFM microrheology measurements were frequency-dependent and fell between the other two methods (Fig. 5B–D, Fig. S10B). The observed increase in apparent Young’s modulus with probing frequency aligns with previous findings on cell stiffening with increased probing rates observed for both AFM indentation (68, 69) and microrheology assays (70–72).”

(4) The plots in Fig.S4 are important as main Figs, particularly given the cartoons of different tissues in Fig.1,2. However, positive correlations for a few genes (CAV1, IGFBP7, TAGLN) are most clear for the multiple lineages that are the same (stomach) or similar (gli, neural & pluri). The authors need to add green lines and pink lines in all plots to indicate the 'lineagespecific' correlations, and provide measures where possible. Some genes clearly don't show the same trends and should be discussed. 

We thank reviewer for this comment. It is indeed an interesting observation (and worth highlighting by adding the fits to lineage-restricted data) that the relationship between relative change in Young’s modulus and the selected gene expression becomes steeper for samples from similar tissue contexts. 

For the sake of keeping the main manuscript compact, we decided to keep Fig. S7 (formerly Fig. S4) in the supplement, however, we did add the linear fit to the glioblastoma dataset (pink line) and a fit to the related neural/embryonic datasets (gli, neural & pluri – purple line) as advised — see below.

We did not pool the stomach data since it is represented by a single point in the figure, aligning with how the data is presented in the main text—stomach adenocarcinoma cell lines (MKN1 and MKN45) are pooled in Fig. 1B (see below).

We have also amended the respective results section to emphasize that, in certain instances, the correlation between changes in mechanical phenotype and alterations in the expression of analysed genes may be less pronounced:

“The relation between normalized apparent Young’s modulus change and fold-change in the expression of the target genes is presented in Fig. S7. The direction of changes in the expression levels between the soft and stiff cell states in the validation datasets was not always following the same direction (Fig. 4, C to F, Fig. S7). This suggests that the genes associated with cell mechanics may not have a monotonic relationship with cell stiffness, but rather are characterized by different expression regimes in which the expression change in opposite directions can have the same effect on cell stiffness. Additionally, in specific cases a relatively high change in Young’s modulus did not correspond to marked expression changes of a given gene — see for example low CAV1 changes observed in MCF10A PIK3CA mutant (Fig. S7A), or low IGFBP7 changes in intestine and lung carcinoma samples (Fig. S7C). This indicates that the importance of specific targets for the mechanical phenotype change may vary depending on the origin of the sample.”

(5) Table-1 neuro: Perhaps I missed the use of the AFM measurements, but these need to be included more clearly in the Results somewhere. 

To clarify: there were no AFM measurements performed for the developing neurons (neuro) dataset, and it is not marked as such in Table 1. There are previously published AFM measurements for the iPSCs dataset (maybe that caused the confusion?), and we referred to them as such in the table by citing the source (Urbanska et al (30)) as opposed to the statement “this paper” (see the last column of Table 1). We did not consider it necessary to include these previously published data. We have added additional horizontal lines to the table that will hopefully help in the table readability.

Reviewer #3 (For Authors) 

Major 

-  I strongly encourage the authors to validate their approach with a gene for which mechanical data does not exist yet, or explore how the combination of the 5 identified genes is the novel regulator of cell mechanics. 

We appreciate the reviewer’s insightful comment and agree that it would be highly interesting to validate further targets and perform combinatorial perturbations. However, it is not feasible at this point to expand the experimental data beyond the one already provided. We hope that in the future, the collective effort of the cell mechanics community will establish more genes that can be used for tuning of mechanical properties of cells.

- If this paper aims at highlighting the power of PC-Corr as a novel inference approach, the authors should compare its predictive power to that of classical co-expression network analysis or an alternative gold standard. 

We thank the reviewer for the suggestion to compare the predictive power of PC-Corr with classical co-expression network analysis or an alternative gold standard. PC-corr has been introduced and characterized in detail in a previous publication (Ciucci et al, 2017, Sci. Rep.), where it was compared against standard co-expression analysis methods. Here we implement PC-corr for a particular application. Thus, we do not see it as central to the message of the present manuscript to compare it with other available methods again.

- The authors call their 5 identified genes "universal, trustworthy and specific". While they provide a great amount of data all is derived from human and mouse cell lines. I suggest toning this down. 

We thank the reviewers for this comment. To clarify, the terms universal, trustworthy and specific are based on the specific hypotheses tested in the validation part of the manuscript, but we understand that it may cause confusion. We have now toned that the statement by adding “universal, trustworthy and specific across the studied mouse and human systems” in the following text fragments:

(1) Abstract

“(…) We validate in silico that the identified gene markers are universal, trustworthy and specific to the mechanical phenotype across the studied mouse and human systems, and demonstrate experimentally that a selected target, CAV1, changes the mechanical phenotype of cells accordingly when silenced or overexpressed. (...)”

(2) Last paragraph of the introduction

“(…) We then test the ability of each gene to classify cell states according to cell stiffness in silico on six further transcriptomic datasets and show that the individual genes, as well as their compression into a combinatorial marker, are universally, specifically and trustworthily associated with the mechanical phenotype across the studied mouse and human systems. (…)”

(3) First paragraph of the discussion

“We provided strong evidence that the inferred conserved functional network module contains an ensemble of five genes that, in particular when combined in a unique combinatorial marker, are universal, specific and trustworthy markers of mechanical phenotype across the studied mouse and human systems.”

Minor suggestions 

-  The authors point out how genes that regulate mechanics often display non-monotonic relations with their mechanical outcome. Indeed, in Fig.4 developing neurons have lower CAV1 in the stiff group. Perturbing CAV1 expression in that model could show the nonmonotonic relation and strengthen their claim. 

We thank reviewer for highlighting this important point. It would indeed be interesting to explore the changes in cell stiffness upon perturbation of CAV1 in a system that has a potential to show an opposing behavior. Unfortunately, we are unable to expand the experimental part of the manuscript at this time. We do hope that this point can be addressed in future research, either by our team or other researchers in the field. 

-  In their gene ontology enrichment assay, the authors claim that their results point towards reduced transcriptional activity and reduced growth/proliferation in stiff compared to soft cells. Proving this with a simple proliferation assay would be a nice addition to the paper. 

This is a valuable suggestion that should be followed up on in detail in the future. To give a preliminary insight into this line of investigation, we have had a look at the cell count data for the CAV1 knock down experiments in TGBC cells. Since CAV1 is associated with the GO Term “negative regulation of proliferation/transcription” (high CAV1 – low proliferation), we would expect that lowering the levels of CAV1 results in increased proliferation and higher cell counts at the end of experiment (3 days post transfection). As illustrated in Author response image 19 below, the cell counts were higher for the samples treated with CAV1 siRNAs, though, not in a statistically significant way. Interestingly, the magnitude of the effect partially mirrored the trends observed for the cell stiffness (Figure 5F).

Author response image 19.

The impact of CAV1 knock down on cell counts in TGBC cells. (A) Absolute cell counts per condition in a 6-well format. Cell counts were performed when harvesting for RT-DC measurements using an automated cell counter (Countess II, Thermo Fisher Scientific). (B) The event rates observed during the RT-DC measurements. The harvested cells are resuspended in a specific volume of measuring buffer standardized per experiment (50-100 μl); thus, the event rates reflect the absolute cell numbers in the respective samples. Horizontal lines delineate medians with mean absolute deviation (MAD) as error, datapoints represent individual measurement replicates, with symbols corresponding to matching measurement days. Statistical analysis was performed using two sample two-sided Wilcoxon rank sum test.

Methods

- The AFM indentation experiments are performed with a very soft cantilever at very high speeds. Why? Also, please mention whether the complete AFM curve was fitted with the Hertz/Sneddon model or only a certain area around the contact point. 

We thank the reviewer for this comment. However, we believe that the spring constants and indentation speeds used in our study are typical for measurements of cells and not a cause of concern. 

For the indentation experiments, we used Arrow-TL1 cantilevers (nominal spring constant k = 0.035-0.045 N m⁻¹, Nanoworld, Switzerland) which are used routinely for cell indentation (with over 200 search results on Google Scholar using the term: "Arrow-TL1"+"cell", and several former publications from our group, including Munder et al 2016, Tavares et al 2017, Urbanska et al 2017, Taubenberger et al 2019, Abuhattum et al 2022, among others). Additionally, cantilevers with the spring constants as low as 0.01 N m−1 can be used for cell measurements (Radmacher 2002, Thomas et al, 2013). 

The indentation speed of 5 µm s⁻¹ is not unusually high and does not result in significant hydrodynamic drag. 

For the microrheology experiments, we used slightly stiffer and shorter (100/200 µm compared to 500 µm for Arrow-TL1) cantilevers: PNP-TR-TL (nominal spring constant k = 0.08 N m⁻¹, Nanoworld, Switzerland). The measurement frequencies of 3-200 Hz correspond to movements slightly faster than 5 µm s⁻¹, but cells were indented only to 100 nm, and the data were corrected for the hydrodynamic drag (see equation (8) in Methods section).

Author response image 20.

Exemplary indentation curve obtained using arrow-TL1 decorated with a 5-µm sphere on a ECC4 cell. The shown plot is exported directly from JPK Data Processing software. The area shaded in grey is the area used for fitting the Sneddon model.  

In the indentation experiments, the curves were fitted to a maximal indentation of 1.5 μm (rarely exceeded, see Author response image 20). We have now added this information to the methods section:

- Could the authors include the dataset wt #1 in Fig 4D? Does it display the same trend? 

We thank the reviewer for this comment. To clarify: in the MCF10A dataset (GEO: GSE69822) there are exactly three replicates of each wt (wild type) and ki (knock-in, referring to the H1047R mutation in the PIK3CA) samples. The numbering wt#2, wt#3, wt#4 originated from the short names that were used in the working files containing non-averaged RPKM (possibly to three different measurement replicates that may have not been exactly paired with the ki samples). We have now renamed the samples as wt#1, wt#2 and wt#3 to avoid the confusion. This naming also reflects better the sample description as deposited in the GSE69822 dataset (see Author response table 2).

Author response table 2.

- Reference (3) is an opinion article with the last author as the sole author. It is used twice as a self-standing reference, which is confusing, as it suggests there is previous experimental evidence. 

We thank the reviewer for pointing this out and agree that it may not be appropriate to cite the article (Guck 2019 Biophysical Reviews, formerly Reference (3), currently Reference (76)) in all instances. The references to this opinion article have now been removed from the introduction:

“The extent to which cells can be deformed by external loads is determined by their mechanical properties, such as cell stiffness. Since the mechanical phenotype of cells has been shown to reflect functional cell changes, it is now well established as a sensitive label-free biophysical marker of cell state in health and disease (1-2).”

“Alternatively, the problem can be reverse-engineered, in that omics datasets for systems with known mechanical phenotype changes are used for prediction of genes involved in the regulation of mechanical phenotype in a mechanomics approach.”

But has been kept in the discussion:

“The mechanical phenotype of cells is recognized as a hallmark of many physiological and pathological processes. Understanding how to control it is a necessary next step that will facilitate exploring the impact of cell mechanics perturbations on cell and tissue function

(76).”.

This reference seems appropriate to us as it expands on the point that our ability to control cell mechanics will enable the exploration of its impact on cell and tissue function, which is central to the discussion of the current manuscript. 

-The authors should mention what PC-corr means. Principle component correlation? Pearson's coefficient correlation? 

PC-corr is a combination of loadings from the principal component (PC) analysis and Pearson’s correlation for each gene pair. We have aimed at conveying this in the “Discriminative network analysis on prediction datasets” result section. We have now added and extra sentence at the first appearance of PC-corr to clarify that for the readers from the start:

“After characterizing the mechanical phenotype of the cell states, we set out to use the accompanying transcriptomic data to elucidate genes associated with the mechanical phenotype changes across the different model systems. To this end, we utilized a method for inferring phenotype-associated functional network modules from omics datasets termed PCCorr (28), that relies on combining loadings obtained from the principal component (PC) analysis and Pearson’s correlation (Corr) for every pair of genes. PC-Corr was performed individually on two prediction datasets, and the obtained results were overlayed to derive a conserved network module. Owing to the combination of the Pearson’s correlation coefficient and the discriminative information included in the PC loadings, the PC-corr analysis does not only consider gene co-expression — as is the case for classical co-expression network analysis — but also incorporates the relative relevance of each feature for discriminating between two or more conditions; in our case, the conditions representing soft and stiff phenotypes. The overlaying of the results from two different datasets allows for a multi-view analysis (utilizing multiple sets of features) and effectively merges the information from two different biological systems.”

- The formatting of Table 1 is confusing. Horizontal lines should be added to make it clear to the reader which datasets are human and which mouse as well as which accession numbers belong to the carcinomas. 

Horizontal lines have now been added to improve the readability of Table 1. We hope that makes the table easier to follow and satisfies the request. We assume that further modifications to the table appearance may occur during publishing process in accordance with the publisher’s guidelines. 

- In many figures, data points are shown in different shapes without an explanation of what the shapes represent. 

We thank the reviewer for this comment and apologize for not adding this information earlier. We have added explanations of the symbols to captions of Figures 2, 3, 5, and 6 in the main text:

“Fig. 2. Mechanical properties of divergent cell states in five biological systems. Schematic overviews of the systems used in our study, alongside with the cell stiffness of individual cell states parametrized by Young’s moduli E. (…) Statistical analysis was performed using generalized linear mixed effects model. The symbol shapes represent measurements of cell lines derived from three different patients (A), matched experimental replicates (C), two different reprogramming series (D), and four different cell isolations (E). Data presented in (A) and (D) were previously published in ref (29) and (30), respectively.”

“Fig. 3. Identification of putative targets involved in cell mechanics regulation. (A) Glioblastoma and iPSC transcriptomes used for the target prediction intersect at 9,452 genes. (B, C) PCA separation along two first principal components of the mechanically distinct cell states in the glioblastoma (B) and iPSC (C) datasets. The analysis was performed using the gene expression data from the intersection presented in (A). The symbol shapes in (B) represent cell lines derived from three different patients. (…)”

“Fig. 5. Perturbing levels of CAV1 affects the mechanical phenotype of intestine carcinoma cells. (…) In (E), (F), (I), and (J), the symbol shapes represent experiment replicates.”

“Fig. 6. Perturbations of CAV1 levels in MCF10A-ER-Src cells result in cell stiffness changes. (…)  Statistical analysis was performed using a two-sided Wilcoxon rank sum test. In (B), (D), and (E), the symbol shapes represent experiment replicates.”

As well as to Figures S2, S9, and S11 in the supplementary material (in Figure S2, the symbol explanation was added to the legends in the figure panels as well): 

“Fig. S2. Plots of area vs deformation for different cell states in the characterized systems. Panels correspond to the following systems: (A) glioblastoma, (B) carcinoma, (C) non-tumorigenic breast epithelia MCF10A, (D) induced pluripotent stem cells (iPSCs), and (E) developing neurons. 95%- and 50% density contours of data pooled from all measurements of given cell state are indicated by shaded areas and continuous lines, respectively. Datapoints indicate medians of individual measurements. The symbol shapes represent cell lines derived from three different patients (A), two different reprogramming series (D), and four different cell isolations (E), as indicated in the respective panels. (…).”

“Fig. S9. CAV1 knock-out mouse embryonic fibroblasts (CAV1KO) have lower stiffness compared to the wild type cells (WT). (…) (C) Apparent Young’s modulus values estimated for WT and CAV1KO cells using areadeformation data in (B). The symbol shapes represent experimental replicates. (…)”

“Fig. S11. Plots of area vs deformation from RT-DC measurements of cells with perturbed CAV1 levels. Panels correspond to the following experiments: (A and B) CAV1 knock-down in TGBC cells using esiRNA (A) and ONTarget siRNA (B), (C and D) transient CAV1 overexpression in ECC4 cells (C) and TGBC cells (D). Datapoints indicate medians of individual measurement replicates. The isoelasticity lines in the background (gray) indicate regions of of same apparent Young’s moduli. The symbol shapes represent experimental replicates.”

- In Figure 2, the difference in stiffness appears bigger than it actually is because the y-axes are not starting at 0. 

While we acknowledge that starting the y-axes at a value other than 0 is generally not ideal, we chose this approach to better display data variability and minimize empty space in the plots.

A similar effect can be achieved with logarithmic scaling, which is a common practice (see  Author response image 21 for visualization). We believe our choice of axes cut-off enhances the interpretability of the data without misleading the viewer.

Author response image 21.

Visualization of different axis scaling strategies applied to the five datasets presented in Figure 2 of the manuscript. 

Of note, apparent Young’s moduli obtained from RT-DC measurements typically span 0.5-3.0 kPa (see Figure 2.3 from Urbanska et al 2021, PhD thesis). Differences between treatments rarely exceed a few hundred pascals. For example, in an siRNA screen of mitotic cell mechanics regulators in Drosophila cells (Kc167), the strongest hits (e.g., Rho1, Rok, dia) showed changes in stiffness of 100-150 Pa (see Supplementary Figure 11 from Rosendahl, Plak et al 2018, Nature Methods 15(5): 355-358).

- In Figure 3, I don't personally see the benefit of showing different cut-offs for PC-corr. In the end, the paper focuses on the 5 genes in the pentagram. I think only showing one of the cutoffs and better explaining why those target genes were picked would be sufficient and make it clearer for the reader. 

We believe it is beneficial to show the extended networks for a few reasons. First, it demonstrates how the selected targets connect to the broader panel of the genes, and that the selected module is indeed much more interconnected than other nodes. Secondly, the chosen PC-corr cut-off is somewhat arbitrary and it may be interesting to look through the genes from the extended network as well, as they are likely also important for regulating cell mechanics. This broader view may help readers identify familiar genes and recognizing the connections to relevant signaling networks and processes of interest.

- In Figure 4C, I suggest explaining why the FANTOM5 and not another dataset was used for the visualization here and mentioning whether the other datasets were similar. 

In Figure 4C, we have chosen to present data corresponding to FANTOM5, because that was the only carcinoma dataset in which all the cell lines tested mechanically are presented. We have now added this information to the caption of Figure 4. Additionally, the clustergrams corresponding to the remaining carcinoma datasets (CCLE RNASeq, Genetech ) are presented in supplementary figures S4-S6. 

“The target genes show clear differences in expression levels between the soft and stiff cell states and provide for clustering of the samples corresponding to different cell stiffnesses in both prediction and validation datasets (Fig. 4, Figs. S4-S6).”

Typos 

We would like to thank the Reviewer#3 for their detailed comments on the typos and details listed below. This is much appreciated as it improved the quality of our manuscript.

-  In the first paragraph of the results section the 'and' should be removed from this sentence: Each dataset encompasses two or more cell states characterized by a distinct mechanical phenotype, and for which transcriptomic data is available. 

The sentence has been corrected and now reads:

“Each dataset encompasses two or more cell states characterized by a distinct mechanical phenotype, and for which transcriptomic data is available.”

-  In the methods in the MCF10A PIK3CA cell lines part, it says cell liens instead of cell lines. 

The sentence has been corrected and now reads:

“The wt cells were additionally supplemented with 10 ng ml⁻¹ EGF (E9644, Sigma-Aldrich), while mutant cell lienes were maintained without EGF.”

-  In the legend of Figure 6 "accession number: GSE17941, data previously published in ())" the reference is missing. 

The reference has been added.

-  In the legend of Figure 5 "(E) Verification of CAV1 knock-down in TGBC cells using two knock-down system" 'a' between using and two is missing. 

The legend has been corrected (no ‘a’ is missing, but it should say systems (plural)):

-  In Figure 5B one horizontal line is missing. 

The Figure 5B has been corrected accordingly. 

-  Terms such as de novo or in silico should be written in cursive. 

We thank the Reviewer for this comment; however, we believe that in the style used by eLife, common Latin expressions such as de novo or in vitro are used in regular font.

-  In the heading of Table 4 "The results presented in this table can be reproducible using the code and data available under the GitHub link reported in the methods section." It should say reproduced instead of reproducible. 

Yes, indeed. It has been corrected.

-  The citation of reference 20 contains several author names multiple times. 

Indeed, it has been fixed now:

-  In Figure S2 there is a vertical line in the zeros of the y axis labels. 

I am not sure if there was some rendering issue, but we did not see a vertical line in the zeros of the y axis label in Figure S2.

- The Text in Figure S4 is too small.                   

We thank the reviewer for pointing this out. We have now revised Figure S7 (formerly Figure S4) to increase the text size, ensuring better readability. (It has also been updated to include additional fits as requested by Reviewer #2).

- In Table 3 "positive hypothesis II markers are discriminative of samples with stiff/soft independent of data source" the words 'mechanical phenotype' are missing. 

The column headings in Table 3 have now been updated accordingly.

- In Table S3 explain in the table headline what vi1, vi2 and v are. I assume the loading for PC1, the loading for PC2 and the average of the previous two values. But it should be mentioned somewhere.

The caption of table S3 has been updated to explain the meaning of vi1, vi2 and v.

Yes. And, I've struggled with detangling "formative" from "summative" ever since I learned them in my graduate training. I have subsequently come to some thoughts that the distinction between these relies heavily on strong links to particular goals/learning outcomes and the available time for the learning experience. The very same assessment can be considered "formative" or "summative" if one changes the goal/LO or the learning timeframe examined. For example, a final exam in CRS 101 is likely to be summative for that course, but may be considered formative for the next course in the curricular sequence (CRS 102) if the major were designed so that the courses seamlessly progressed from one to the next.

memex personal computer

memory and index

not just interpersonal but interplanetary and local firsst autonomous private secure permanenet evergreen

will be a new profession of trailblazers who will make a career out of finding useful trails through the common record.

not just finding but naming and creating/namng trails linking meaningfully the personal and collaboratively emerging interintellect in grounded in individuals indranet.work spaces

indy.memex interpersonal computer

spiritual reparenting

This section makes me reflect on the common misconception that tools like GenAI or even Google can replace human knowledge. As an educator, I see how tempting it might be for students (and even teachers) to rely heavily on these tools, but this dependency can create significant gaps in critical thinking and problem-solving. The quote about interpreting information resonates with me because technology can provide data, but understanding and applying it require skills and context that only humans bring.

Personally, I agree with the statement that solving complex problems requires more than just finding information online. It reminds me of situations in my professional role where I’ve had to assess the validity of data or consider the nuances of a problem—something no search engine or AI can do without my input and expertise. GenAI can be a powerful assistant, but the “knowledge in our head” is what allows us to navigate ambiguity and discern quality.

I wonder if relying too much on tools like ChatGPT might weaken students’ ability to critically evaluate information or even know where to start when they don’t have a foundation of knowledge. While GenAI can support learning, I see a real danger if we let it replace the essential process of building and applying our understanding. What do you think—is there a way to balance using these tools without diminishing the development of core skills?

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

(1) As VRMate (a component of behaviorMate) is written using Unity, what is the main advantage of using behaviorMate/VRMate compared to using Unity alone paired with Arduinos (e.g. Campbell et al. 2018), or compared to using an existing toolbox to interface with Unity (e.g. Alsbury-Nealy et al. 2022, DOI: 10.3758/s13428-021-01664-9)? For instance, one disadvantage of using Unity alone is that it requires programming in C# to code the task logic. It was not entirely clear whether VRMate circumvents this disadvantage somehow -- does it allow customization of task logic and scenery in the GUI? Does VRMate add other features and/or usability compared to Unity alone? It would be helpful if the authors could expand on this topic briefly.

We have updated the manuscript (lines 412-422) to clarify the benefits of separating the VR system as an isolated program and a UI that can be run independently. We argue that “…the recommended behaviorMate architecture has several important advantages. Firstly, by rendering each viewing angle of a scene on a dedicated device, performance is improved by splitting the computational costs across several inexpensive devices rather than requiring specialized or expensive graphics cards in order to run…, the overall system becomes more modular and easier to debug [and] implementing task logic in Unity would require understanding Object-Oriented Programming and C# … which is not always accessible to researchers that are typically more familiar with scripting in Python and Matlab.”

VRMate receives detailed configuration info from behaviorMate at runtime as to which VR objects to display and receives position updates during experiments. Any other necessary information about triggering rewards or presenting non-VR cues is still handled by the UI so no editing of Unity is necessary. Scene configuration information is in the same JSON format as the settings files for behaviorMate, additionally there are Unity Editor scripts which are provided in the VRmate repository which permit customizing scenes through a “drag and drop” interface and then writing the scene configuration files programmatically. Users interested in these features should see our github page to find example scene.vr files and download the VRMate repository (including the editor scripts).  We provided 4 vr contexts, as well as a settings file that uses one of them which can be found on the behaviorMate github page (https://github.com/losonczylab/behaviorMate) in the “vr_contexts” and “example_settigs_files” directories. These examples are provided to assist VRMate users in getting set up and could provide a more detailed example of how VRMate and behaviorMate interact.

(2) The section on "context lists", lines 163-186, seemed to describe an important component of the system, but this section was challenging to follow and readers may find the terminology confusing. Perhaps this section could benefit from an accompanying figure or flow chart, if these terms are important to understand.

We maintain the use of the term context and context list in order to maintain a degree of parity with the java code. However, we have updated lines 173-175 to define the term context for the behaviorMate system: “... a context is grouping of one or more stimuli that get activated concurrently. For many experiments it is desirable to have multiple contexts that are triggered at various locations and times in order to construct distinct or novel environments.”

a. Relatedly, "context" is used to refer to both when the animal enters a particular state in the task like a reward zone ("reward context", line 447) and also to describe a set of characteristics of an environment (Figure 3G), akin to how "context" is often used in the navigation literature. To avoid confusion, one possibility would be to use "environment" instead of "context" in Figure 3G, and/or consider using a word like "state" instead of "context" when referring to the activation of different stimuli.

Thank you for the suggestion. We have updated Figure 3G to say “Environment” in order to avoid confusion.

(3) Given the authors' goal of providing a system that is easily synchronizable with neural data acquisition, especially with 2-photon imaging, I wonder if they could expand on the following features:

a. The authors mention that behaviorMate can send a TTL to trigger scanning on the 2P scope (line 202), which is a very useful feature. Can it also easily generate a TTL for each frame of the VR display and/or each sample of the animal's movement? Such TTLs can be critical for synchronizing the imaging with behavior and accounting for variability in the VR frame rate or sampling rate.

Different experimental demands require varying levels of precision in this kind of synchronization signals. For this reason, we have opted against a “one-size fits all” for synchronization with physiology data in behaviorMate. Importantly this keeps the individual rig costs low which can be useful when constructing setups specifically for use when training animals. behaviorMate will log TTL pulses sent to GPIO pins setup as sensors, and can be configured to generate TTL pulses at regular intervals. Additionally all UDP packets received by the UI are time stamped and logged. We also include the output of the arduino millis() function in all UDP packets which can be used for further investigation of clock drift between system components. Importantly, since the system is event driven there cannot be accumulating drift across running experiments between the behaviorMate UI and networked components such as the VR system.

For these reasons, we have not needed to implement a VR frame synchronization TTL for any of our experiments, however, one could extend VRMate to send "sync" packets back to behaviorMate to log when each frame was displayed precisely or TTL pulses (if using the same ODROID hardware we recommend in the standard setup for rendering scenes). This would be useful if it is important to account for slight changes in the frame rate at which the scenes are displayed. However, splitting rendering of large scenes between several devices results in fast update times and our testing and benchmarks indicate that display updates are smooth and continuous enough to appear coupled to movement updates from the behavioral apparatus and sufficient for engaging navigational circuits in the brain.

b. Is there a limit to the number of I/O ports on the system? This might be worth explicitly mentioning.

We have updated lines 219-220 in the manuscript to provide this information: Sensors and actuators can be connected to the controller using one of the 13 digital or 5 analog input/output connectors.

c. In the VR version, if each display is run by a separate Android computer, is there any risk of clock drift between displays? Or is this circumvented by centralized control of the rendering onset via the "real-time computer"?

This risk is mitigated by the real-time computer/UI sending position updates to the VR displays. The maximum amount scenes can be out of sync is limited because they will all recalibrate on every position update – which occurs multiple times per second as the animal is moving. Moreover, because position updates are constantly being sent by behaviorMate to VRMate and VRMate is immediately updating the scene according to this position, the most the scene can become out of sync with the mouse's position is proportional to the maximum latency multiplied by the running speed of the mouse. For experiments focusing on eliciting an experience of navigation, such a degree of asynchrony is almost always negligible. For other experimental demands it could be possible to incorporate more precise frame timing information but this was not necessary for our use case and likely for most other use cases. Additionally, refer to the response to comment 3a.

Reviewer #2 (Public review):

(1) The central controlling logic is coupled with GUI and an event loop, without a documented plugin system. It's not clear whether arbitrary code can be executed together with the GUI, hence it's not clear how much the functionality of the GUI can be easily extended without substantial change to the source code of the GUI. For example, if the user wants to perform custom real-time analysis on the behavior data (potentially for closed-loop stimulation), it's not clear how to easily incorporate the analysis into the main GUI/control program.

Without any edits to the existing source code behaviorMate is highly customizable through the settings files, which allow users to combine the existing contexts and decorators in arbitrary combinations. Therefore, users have been able to perform a wide variety of 1D navigation tasks, well beyond our anticipated use cases by generating novel settings files. The typical method for providing closed-loop stimulation would be to set up a context which is triggered by animal behavior using decorators (e.g. based on position, lap number and time) and then trigger the stimulation with a TTL pulse. Rarely, if users require a behavioral condition not currently implemented or composable out of existing decorators, it would require generating custom code in Java to extend the UI. Performing such edits requires only knowledge of basic object-oriented programming in Java and generating a single subclass of either the BasicContextList or ContextListDecorator classes. In addition, the JavaFX (under development) version of behaviorMate incorporates a plugin which doesn't require recompiling the code in order to make these changes. However, since the JavaFX software is currently under development, documentation does not yet exist. All software is open-sourced and available on github.com for users interested in generating plugins or altering the source code.

We have added the additional caveat to the manuscript in order to clarify this point (Line 197-202): “However, if the available set of decorators is not enough to implement the required task logic, some modifications to the source code may be necessary. These modifications, in most cases, would be very simple and only a basic understanding of object-oriented programming is required. A case where this might be needed would be performing novel customized real-time analysis on behavior data and activating a stimulus based on the result”

(2) The JSON messaging protocol lacks API documentation. It's not clear what the exact syntax is, supported key/value pairs, and expected response/behavior of the JSON messages. Hence, it's not clear how to develop new hardware that can communicate with the behaviorMate system.

The most common approach for adding novel hardware is to use TTL pulses (or accept an emitted TTL pulse to read sensor states). This type of hardware addition  is possible through the existing GPIO without the need to interact with the software or JSON API. Users looking to take advantage of the ability to set up and configure novel behavioral paradigms without the need to write any software would be limited to adding hardware which could be triggered with and report to the UI with a TTL pulse (however fairly complex actions could be triggered this way).

For users looking to develop more customized hardware solutions that interact closely with the UI or GPIO board, additional documentation on the JSON messaging protocol has been added to the behaviormate-utils repository (https://github.com/losonczylab/behaviormate_utils). Additionally, we have added a link to this repository in the Supplemental Materials section (line 971) and referenced this in the manuscript (line 217) to make it easier for readers to find this information.

Furthermore, developers looking to add completely novel components to the UI  can implement the interface described by Context.java in order to exchange custom messages with hardware. (described  in the JavaDoc: https://www.losonczylab.org/behaviorMate-1.0.0/)  These messages would be defined within the custom context and interact with the custom hardware (meaning the interested developer would make a novel addition to the messaging API). Additionally, it should be noted that without editing any software, any UDP packets sent to behaviorMate from an IP address specified in the settings will get time stamped and logged in the stored behavioral data file meaning that are a large variety of hardware implementation solutions using both standard UDP messaging and through TTL pulses that can work with behaviorMate with minimal effort. Finally, see response to R2.1 for a discussion of the JavaFX version of the behaviorMatee UI including plugin support.

(3) It seems the existing control hardware and the JSON messaging only support GPIO/TTL types of input/output, which limits the applicability of the system to more complicated sensor/controller hardware. The authors mentioned that hardware like Arduino natively supports serial protocols like I2C or SPI, but it's not clear how they are handled and translated to JSON messages.

We provide an implementation for an I2C-based capacitance lick detector which interested developers may wish to copy if support for novel I2C or SPI. Users with less development experience wishing to expand the hardware capabilities of  behaviorMatecould also develop adapters which can be triggered  on a TTL input/output. Additionally, more information about the JSON API and how messages are transmitted to the PC by the arduino is described in point (2) and the expanded online documentation.

a. Additionally, because it's unclear how easy to incorporate arbitrary hardware with behaviorMate, the "Intranet of things" approach seems to lose attraction. Since currently, the manuscript focuses mainly on a specific set of hardware designed for a specific type of experiment, it's not clear what are the advantages of implementing communication over a local network as opposed to the typical connections using USB.

As opposed to serial communication protocols as typical with USB, networking protocols seamlessly function based on asynchronous message passing. Messages may be routed internally (e.g. to a PCs localhost address, i.e. 0.0.0..0) or to a variety of external hardware (e.g. using IP addresses such as those in the range 192.168.1.2 - 192.168.1.254). Furthermore, network-based communication allows modules, such as VR, to be added easily. behavoirMate systems can be easily expanded using low-cost Ethernet switches and consume only a single network adapter on the PC (e.g. not limited by the number of physical USB ports). Furthermore, UDP message passing is implemented in almost all modern programming languages in a platform independent manner (meaning that the same software can run on OSX, Windows, and Linux). Lastly, as we have pointed out (Line 117) a variety of tools exist for inspecting network packets and debugging; meaning that it is possible to run behaviorMate with simulated hardware for testing and debugging.

The IOT nature of behaviorMate means there is no requirement for novel hardware to be implemented  using an arduino,  since any system capable of  UDP communication can  be configured. For example, VRMate is usually run on Odroid C4s, however one could easily create a system using Raspberry Pis or even additional PCs. behaviorMate is agnostic to the format of the UDP messages, but packaging any data in the JSON format for consistency would be encouraged. If a new hardware is a sensor that has input requiring it to be time stamped and logged then all that is needed is to add the IP address and port information to the ‘controllers’ list in a behaviorMate settings file. If more complex interactions are needed with novel hardware than a custom implementation of ContextList.java may be required (see response to R2.2). However, the provided UdpComms.java class could be used to easily send/receive messages from custom Context.java subclasses.

Solutions for highly customized hardware do require basic familiarity with object-oriented programming using the Java programming language. However, in our experience most behavioral experiments do not require these kinds of modifications. The majority of 1D navigation tasks, which behaviorMate is currently best suited to control, require touch/motion sensors, LEDs, speakers, or solenoid valves,  which are easily controlled by the existing GPIO implementation. It is unlikely that custom subclasses would even be needed.

Reviewer #3 (Public review):

(1) While using UDP for data transmission can enhance speed, it is thought that it lacks reliability. Are there error-checking mechanisms in place to ensure reliable communication, given its criticality alongside speed?

The provided GPIO/behavior controller implementation sends acknowledgement packets in response to all incoming messages as well as start and stop messages for contexts and “valves”. In this way the UI can update to reflect both requested state changes as well as when they actually happen (although there is rarely a perceptible gap between these two states unless something is unplugged or not functioning). See Line 85 in the revised manuscript “acknowledgement packets are used to ensure reliable message delivery to and from connected hardware”.

(2) Considering this year's price policy changes in Unity, could this impact the system's operations?

VRMate is not affected by the recent changes in pricing structure of the Unity project.

The existing compiled VRMate software does not need to be regenerated to update VR scenes, or implement new task logic (since this is handled by the behaviorMate GUI). Therefore, the VRMate program is robust to any future pricing changes or other restructuring of the Unity program and does not rely on continued support of Unity. Additionally, while the solution presented in VRMate has many benefits, a developer could easily adapt any open-source VR Maze project to receive the UDP-based position updates from behaviorMate or develop their own novel VR solutions.

(3) Also, does the Arduino offer sufficient precision for ephys recording, particularly with a 10ms check?

Electrophysiology recording hardware typically has additional I/O channels which can provide assistance with tracking behavior/synchronization at a high resolution. While behaviorMate could still be used to trigger reward valves, either the ephys hardware or some additional high-speed DAQ would be recommended to maintain accurately with high-speed physiology data. behaviorMate could still be set up as normal to provide closed and open-loop task control at behaviorally relevant timescales alongside a DAQ circuit recording events at a consistent temporal resolution. While this would increase the relative cost of the individual recording setup, identical rigs for training animals could still be configured without the DAQ circuit avoiding unnecessary cost and complexity.

(4) Could you clarify the purpose of the Sync Pulse? In line 291, it suggests additional cues (potentially represented by the Sync Pulse) are needed to align the treadmill screens, which appear to be directed towards the Real-Time computer. Given that event alignment occurs in the GPIO, the connection of the Sync Pulse to the Real-Time Controller in Figure 1 seems confusing.

A number of methods exist for synchronizing recording devices like microscopes or electrophysiology recordings with behaviorMate’s time-stamped logs of actuators and sensors. For example, the GPIO circuit can be configured to send sync triggers, or receive timing signals as input. Alternatively a dedicated circuit could record frame start signals and relay them to the PC to be logged independently of the GPIO (enabling a high-resolution post-hoc alignment of the time stamps). The optimal method to use varies based on the needs of the experiment. Our setups have a dedicated BNC output and specification in the settings file that sends a TTL pulse at the start of an experiment in order to trigger 2p imaging setups (see line 224, specifically that this is a detail of “our” 2p imaging setup). We provide this information as it might be useful suggesting how to have both behavior and physiology data start recording at the same time. We do not intend this to be the only solution for alignment. Figure 1 indicates an “optional” circuit for capturing a high speed sync pulse and providing time stamps back to the real time PC. This is another option that might be useful for certain setups (or especially for establishing benchmarks between behavior and physiology recordings). In our setup event alignment does not exclusively occur on the GPIO.

a. Additionally, why is there a separate circuit for the treadmill that connects to the UI computer instead of the GPIO? It might be beneficial to elaborate on the rationale behind this decision in line 260.

Event alignment does not occur on the GPIO, separating concerns between position tracking and more general input/output features which improves performance and simplifies debugging.  In this sense we maintain a single event loop on the Arduino, avoiding the need to either run multithreaded operations or rely extensively on interrupts which can cause unpredictable code execution (e.g. when multiple interrupts occur at the same time). Our position tracking circuit is therefore coupled to a separate,low-cost arduino mini which has the singular responsibility of position-tracking.

b. Moreover, should scenarios involving pupil and body camera recordings connect to the Analog input in the PCB or the real-time computer for optimal data handling and processing?

Pupil and body camera recordings would be independent data streams which can be recorded separately from behaviorMate. Aligning these forms of full motion video could require frame triggers which could be configured on the GPIO board using single TTL like outputs or by configuring a valve to be “pulsed” which is a provided type customization.

We also note that a more advanced developer could easily leverage camera signals to provide closed loop control by writing an independent module that sends UDP packets to behavoirMate. For example a separate computer vision based position tracking module could be written in any preferred language and use UDP messaging to send body tracking updates to the UI without editing any of the behaviorMate source code (and even used for updating 1D location).

(5) Given that all references, as far as I can see, come from the same lab, are there other labs capable of implementing this system at a similar optimal level?

To date two additional labs have published using behaviorMate, the Soltez and Henn labs (see revised lines 341-342). Since behaviorMate has only recently been published and made available open source, only external collaborators of the Losonczy lab have had access to the software and design files needed to do this. These collaborators did, however, set up their own behavioral setups in separate locations with minimal direct support from the authors–similar to what would be available to anyone seeking to set a behaviorMate system would find online on our github page or by posting to the message board.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(4) To provide additional context for the significance of this work, additional citations would be helpful to demonstrate a ubiquitous need for a system like behaviorMate. This was most needed in the paragraph from lines 46-65, specifically for each sentence after line 55, where the authors discuss existing variants on head-fixed behavioral paradigms. For instance, for the clause "but olfactory and auditory stimuli have also been utilized at regular virtual distance intervals to enrich the experience with more salient cues", suggested citations include Radvansky & Dombeck 2018 (DOI: 10.1038/s41467-018-03262-4), Fischler-Ruiz et al. 2021 (DOI: 10.1016/j.neuron.2021.09.055).

We thank the reviewer for the suggested missing citations and have updated the manuscript accordingly (see line 58).

(5) In addition, it would also be helpful to clarify behaviorMate's implementation in other laboratories. On line 304 the authors mention "other labs" but the following list of citations is almost exclusively from the Losonczy lab. Perhaps the citations just need to be split across the sentence for clarity? E.g. "has been validated by our experimental paradigms" (citation set 1) "and successfully implemented in other labs as well" (citation set 2).

We have split the citation set as suggested (see lines 338-342).

Minor Comments:

(6) In the paragraph starting line 153 and in Fig. 2, please clarify what is meant by "trial" vs. "experiment". In many navigational tasks, "trial" refers to an individual lap in the environment, but here "trial" seems to refer to the whole behavioral session (i.e. synonymous with "experiment"?).

In our software implementation we had originally used “trial” to refer to an imaging session rather than experiment (and have made updates to start moving to the more conventional lexicon). To avoid confusion we have remove this use of “trial” throughout the manuscript and replaced with “experiment” whenever possible

(7) This is very minor, but in Figure 3 and 4, I don't believe the gavage needle is actually shown in the image. This is likely to avoid clutter but might be confusing to some readers, so it may be helpful to have a small inset diagram showing how the needle would be mounted.

We assessed the image both with and without the gavage needle and found the version in the original (without) to be easier to read and less cluttered and therefore maintained that version in the manuscript.

(8) In Figure 5 legend, please list n for mice and cells.

We have updated the Figure 5 legend to indicate that for panels C-G, n=6 mice (all mice were recorded in both VR and TM systems), 3253 cells in VR classified as significantly tuned place cells VR, and 6101 tuned cells in TM,

(9) Line 414: It is not necessary to tilt the entire animal and running wheel as long as the head-bar clamp and objective can rotate to align the imaging window with the objective's plane of focus. Perhaps the authors can just clarify the availability of this option if users have a microscope with a rotatable objective/scan head.

We have added the suggested caveat to the manuscript in order to clarify when the goniometers might be useful (see lines 281-288).

(10) Figure S1 and S2 could be referenced explicitly in the main text with their related main figures.

We have added explicit references to figures S1 and S2 in the relevant sections (see lines 443, 460  and 570)

(11) On line 532-533, is there a citation for "proximal visual cues and tactile cues (which are speculated to be more salient than visual cues)"?

We have added citations to both Knierim & Rao 2003 and Renaudineau et al. 2007 which discuss the differential impact of proximal vs distal cues during navigation as well as Sofroniew et al. 2014 which describe how mice navigate more naturally in a tactile VR setup as opposed to purely visual ones.

(12) There is a typo at the end of the Figure 2 legend, where it should say "Arduino Mini."

This typo has been fixed.

Reviewer #2 (Recommendations For The Authors):

(4) As mentioned in the public review: what is the major advantage of taking the IoT approaches as opposed to USB connections to the host computer, especially when behaviorMate relies on a central master computer regardless? The authors mentioned the readability of the JSON messages, making the system easier to debug. However, the flip side of that is the efficiency of data transmission. Although the bandwidth/latency is usually more than enough for transmitting data and commands for behavior devices, the efficiency may become a problem when neural recording devices (imaging or electrophysiology) need to be included in the system.

behaviorMate is not intended to do everything, and is limited to mainly controlling behavior and providing some synchronizing TTL style triggers. In this way the system can easily and inexpensively be replicated across multiple recording setups; particularly this is useful for constructing additional animal training setups. The system is very much sufficient for capturing behavioral inputs at relevant timescales (see the benchmarks in Figures 3 and 4 as well as the position correlated neural activity in Figures 5 and 6 for demonstration of this). Additional hardware might be needed to align the behaviorMate output with neural data for example a high-speed DAQ or input channels on electrophysiology recording setups could be utilized (if provided). As all recording setups are different the ideal solution would depend on details which are hard to anticipate. We do not mean to convey that the full neural data would be transmitted to the behaviorMate system (especially using the JSON/UDP communications that behaviorMate relies on).

(5) The author mentioned labView. A popular open-source alternative is bonsai (https://github.com/bonsai-rx/bonsai). Both include a graphical-based programming interface that allows the users to easily reconfigure the hardware system, which behaviorMate seems to lack. Additionally, autopilot (https://github.com/auto-pi-lot/autopilot) is a very relevant project that utilizes a local network for multiple behavior devices but focuses more on P2P communication and rigorously defines the API/schema/communication protocols for devices to be compatible. I think it's important to include a discussion on how behaviorMate compares to previous works like these, especially what new features behaviorMate introduces.

We believe that behaviorMate provides a more opinionated and complete solution than the projects mentioned. A wide variety of 1D navigational paradigms can be constructed in behaviorMate without the need to write any novel software. For example, bonsai is a “visual programming language” and would require experimenters to construct a custom implementation of each of their experiments. We have opted to use Java for the UI with distributed computations across modules in various languages. Given the IOT methodology it would be possible to use any number of programming languages or APIs; a large number of design decisions were made  when building the project and we have opted to not include this level of detail in the manuscript in order to maintain readability. We strongly believe in using non-proprietary and open source projects, when possible, which is why the comparison with LabView based solutions was included in the introduction. Also, we have added a reference to the autopilot reference to the section of the introduction where this is discussed.

(6) One of the reasons labView/bonsai are popular is they are inherently parallel and can simultaneously respond to events from different hardware sources. While the JSON events in behaviorMate are asynchronous in nature, the handling of those events seems to happen only in a main event loop coupled with GUI, which is sequential by nature. Is there any multi-threading/multi-processing capability of behaviorMate? If so it's an important feature to highlight. If not I think it's important to discuss the potential limitation of the current implementation.

IOT solutions are inherently concurrent since the computation is distributed. Additional parallelism could be added by further distributing concerns between additional independent modules running on independent hardware. The UI has an eventloop which aggregates inputs and then updates contexts based on the current state of those inputs sequentially. This sort of a “snapshot” of the current state is necessary to reason about when the start certain contexts based on their settings and applied decorators. While the behaviorMate UI uses multithreading libraries in Java to be more performant in certain cases, the degree to which this represents true vs “virtual” concurrency would depend on the individual PC architecture it is run on and how the operating system allocates resources. For this reason, we have argued in the manuscript that behaviorMate is sufficient for controlling experiments at behaviorally relevant timescales, and have presented both benchmarks and discussed different synchronization approaches and permit users to determine if this is sufficient for their needs.

(7) The context list is an interesting and innovative approach to abstract behavior contingencies into a data structure, but it's not currently discussed in depth. I think it's worth highlighting how the context list can be used to cover a wide range of common behavior experimental contingencies with detailed examples (line 185 might be a good example to give). It's also important to discuss the limitation, as currently the context lists seem to only support contingencies based purely on space and time, without support for more complicated behavior metrics (e.g. deliver reward only after X% correct).

To access more complex behavior metrics during runtime, custom context list decorators would need to be implemented. While this is less common in the sort of 1D navigational behaviors the project was originally designed to control, adding novel decorators is a simple process that only requires basic object oriented programming knowledge. As discussed we are also implementing a plugin-architecture in the JavaFX update to streamline these types of additions.

Minor Comments:

(8) In line 202, the author suggests that a single TTL pulse is sent to mark the start of a recording session, and this is used to synchronize behavior data with imaging data later. In other words, there are no synchronization signals for every single sample/frame. This approach either assumes the behavior recording and imaging are running on the same clock or assumes evenly distributed recording samples over the whole recording period. Is this the case? If so, please include a discussion on limitations and alternative approaches supported by behaviorMate. If not, please clarify how exactly synchronization is done with one TTL pulse.

While the TTL pulse triggers the start of neural data in our setups, various options exist for controlling for the described clock drift across experiments and the appropriate one depends on the type of recordings made, frame rate duration of recording etc. Therefore behaviorMate leaves open many options for synchronization at different time scales (e.g. the adding a frame-sync circuit as shown in Figure 1 or sending TTL pulses to the same DAQ recording electrophysiology data).  Expanded consideration of different synchronization methods has been included in the manuscript (see lines 224-238).

(9) Is the computer vision-based calibration included as part of the GUI functionality? Please clarify. If it is part of the GUI, it's worth highlighting as a very useful feature.

The computer vision-based benchmarking is not included in the GUI. It is in the form of a script made specifically for this paper. However for treadmill-based experiments behaviorMate has other calibration tools built into it (see line 301-303).

(10) I went through the source code of the Arduino firmware, and it seems most "open X for Y duration" functions are implemented using the delay function. If this is indeed the case, it's generally a bad idea since delay completely pauses the execution and any events happening during the delay period may be missed. As an alternative, please consider approaches comparing timestamps or using interrupts.

We have avoided the use of interrupts on the GPIO due to the potential for unpredictable code execution. There is a delay which is only just executed if the duration is 10 ms or less as we cannot guarantee precision of the arduino eventloop cycling faster than this. Durations longer than 10 ms would be time stamped and non-blocking. We have adjusted this MAX_WAIT to be specified as a macro so it can be more easily adjusted (or set to 0).

(11) Figure 3 B, C, D, and Figure 4 D, E suffer from noticeable low resolution.

We have converted Figure 3B, C, D and 4C, D, E to vector graphics in order to improve the resolution.

(12) Figure 4C is missing, which is an important figure.

This figure appeared when we rendered and submitted the manuscript. We apologize if the figure was generated such that it did not load properly in all pdf viewers. The panel appears correctly in the online eLife version of the manuscript. Additionally, we have checked the revision in Preview on Mac OS as well as Adobe Acrobat and the built-in viewer in Chrome and all figure panels appear in each so we hope this issue has been resolved.

(13) There are thin white grid lines on all heatmaps. I don't think they are necessary.

The grid lines have been removed from the heatmaps  as suggested.

(14) Line 562 "sometimes devices directly communicate with each other for performance reasons", I didn't find any elaboration on the P2P communication in the main text. This is potentially worth highlighting as it's one of the advantages of taking the IoT approaches.

In our implementation it was not necessary to rely on P2P communication beyond what is indicated in Figure 1. The direct communication referred to in line 562 is meant only to refer to the examples expanded on in the rest of the paragraph i.e. the behavior controller may signal the microscope directly using a TTL signal without looping back to the UI. As necessary users could implement UDP message passing between devices, but this is outside the scope of what we present in the manuscript.

(15) Line 147 "Notably, due to the systems modular architecture, different UIs could be implemented in any programming language and swapped in without impacting the rest of the system.", this claim feels unsupported without a detailed discussion of how new code can be incorporated in the GUI (plugin system).

This comment refers to the idea of implementing “different UIs”. This would entail users desiring to take advantage of the JSON messaging API and the proposed electronics while fully implementing their own interface. In order to facilitate this option we have improved documentation of the messaging API posted in the README file accompanying the arduino source code. We have added reference to the supplemental materials where readers can find a link to the JSON API implementation to clarify this point.

Additionally, while a plugin system is available in the JavaFX version of behaviorMate, this project is currently under development and will update the online documentation as this project matures, but is unrelated to the intended claim about completely swapping out the UI.

Reviewer #3 (Recommendations For The Authors):

(6) Figure 1 - the terminology for each item is slightly different in the text and the figure. I think making the exact match can make it easier for the reader.

- Real-time computer (figure) vs real-time controller (ln88).

The manuscript was adjusted to match figure terminology.

- The position controller (ln565) - position tracking (Figure).

We have updated Figure 1 to highlight that the position controller does the position tracking.

- Maybe add a Behavior Controller next to the GPIO box in Figure 1.

We updated Figure 1 to highlight that the Behavior Controller performs the GPIO responsibility such that "Behavior Controller" and "GPIO circuit" may be used interchangeably.

- Position tracking (fig) and position controller (subtitle - ln209).

We updated Figure 1 to highlight that the position controller does the position tracking.

- Sync Pulse is not explained in the text.

The caption for Figure 1 has been updated to better explain the Sync pulse and additional systems boxes

(7) For Figure 3B/C: What is the number of data points? It would be nice to see the real population, possibly using a swarm plot instead of box plots. How likely are these outliers to occur?

In order to better characterize the distributions presented in our benchmarking data we have added mean and standard deviation information the plots 3 and 4. For Figure 3B: 0.0025 +/- 0.1128, Figure 3C: 12.9749 +/- 7.6581, Figure 4C: 66.0500 +/- 15.6994, Figure 4E: 4.1258 +/- 3.2558.

Author response:

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

Reviewer #1 (Public Review):

Time periods in which experience regulates early plasticity in sensory circuits are well established, but the mechanisms that control these critical periods are poorly understood. In this manuscript, Leier and Foden and colleagues examine early-life critical periods that regulate the Drosophila antennal lobe, a model sensory circuit for understanding synaptic organization. Using early-life (0-2 days old) exposure to distinct odorants, they show that constant odor exposure markedly reduces the volume, synapse number, and function of the VM7 glomerulus. The authors offer evidence that these changes are mediated by invasion of ensheathing glia into the glomerulus where they phagocytose connections via a mechanism involving the engulfment receptor Draper.

This manuscript is a striking example of a study where the questions are interesting, the authors spent a considerable amount of time to clearly think out the best experiments to ask their questions in the most straightforward way, and expressed the results in a careful, cogent, and well-written fashion. It was a genuine delight to read this paper. I have two experimental suggestions that would really round out existing work to better support the existing conclusions and some instances where additional data or tempered language in describing results would better support their conclusions. Overall, though, this is an incredibly important finding, a careful analysis, and an excellent mechanistic advance in understanding sensory critical period biology.

We thank the reviewer for their thoughtful and constructive comments on our manuscript. In response to their critiques, we conducted several new experiments as well as additional analysis and making changes to the text. As requested, we carried out an electrophysiological analysis of VM7 PN firing in draper knockdown animals with and without odor exposure. To our surprise, loss of glial Draper fully suppresses the dramatic reduction in spontaneous PN activity observed following critical period ethyl butyrate exposure, arguing that the functional response is restored alongside OSN morphology. It also suggests that the OR42a OSN terminals are intact and functional until they are phagocytosed by ensheathing glia. In other words, glia are not merely clearing axon terminals that have already degenerated. This evidence provides additional support to the claim that the VM7 glomerulus will be an outstanding model for defining mechanism of experience-dependent glial pruning. Detailed responses to the reviewers’ comments follow below. 

Regarding the apparent disconnect between the near complete silencing of PNs versus the 50% reduction in OR42a OSN infiltration volume, we agree with the reviewer that this tracks with previous data in the field. While our Imaris pipeline is relatively sensitive, it may not pick up modest changes to terminal arbor architecture. Indeed, as described in Jindal et al. (2023) and in the Methods in this manuscript, we chose conservative software settings that, if anything, would undercount the percent change in infiltration volume. We also note that increased inhibitory LN inputs onto PNs could contribute to dramatic PN silencing we observe. While fascinating, we view LN plasticity beyond the scope of the current manuscript. We removed any mention of ‘silent synapses’ and now speculate about increased inhibition. 

Reviewer #1 (Recommendations For The Authors):

Major Elements:

(1) The authors demonstrate that loss of draper in glia can suppress many of the pruning related phenotypes associated with EB exposure. However, they do not assess electrophysiological output in these experiments, only morphology. It would be great to see recordings from those animals to see if the functional response is also restored.

We performed the experiment the reviewer requested (see Figure 4F-J). We are pleased to report that our recordings from VM7 PNs match our morphology measurements: in repo-GAL4>UAS-draper RNAi flies, there was no difference in the innervation of VM7 PNs between animals exposed to mineral oil or 15% EB from 0-2 DPE. This result is in sharp contrast to the near-total loss of OSN-PN innervation in flies with intact glial Draper signaling, and strongly validates the role we propose for Draper in the Or42a OSN critical period.

(2) There is a disconnect between physiology and morphology with a near complete loss of activity from VM7 PNs but a less severe loss of ORN synapses. While not completely incongruent (previous work in the AL showed a complete loss of attractive behavior though synapse number was only reduced 40% - Mosca et al. 2017, eLife), it is curious. Can the authors comment further? Ideally, some of these synapses could be visualized by EM to determine if the remaining synapses are indeed of correct morphology. If not, this could support their assertion of silent inputs from page 7. Further, what happens to the remaining synapses? VM7 PNs should be receiving some activity from other local interneurons as well as neighboring PNs.

We agree that on the surface, our electrophysiology results are more striking than one might expect solely from our measurements of VM7 morphology and presynaptic content. As the reviewer points out, previous studies of fly olfaction have consistently found that relatively modest shifts in glomerular volume in response to prolonged earlylife odorant exposure can be accompanied by drastic changes in physiology and behavior (in addition, we would add Devaud et al., 2003; Devaud et al., 2001; Acebes et al., 2012; and Chodankar et al., 2020, as foundational examples of this phenomenon). 

A major driver of these changes appears to be remodeling of antennal lobe inhibitory LNs (see Das et al., 2011; Wilson and Laurent, 2005; Chodankar et al., 2020), especially GABAergic inhibitory interneurons. Perhaps increased LN inhibition of chronically activated PNs, on top of the reduced excitatory inputs resulting from ensheathing glial pruning of the Or42a OSN terminal arbor, would explain the near-total loss of VM7 PN activity we observe after critical period EB exposure. However, given that the scope of our study is limited to critical-period glial biology and does not address the complex topics of LN rewiring or synapse morphology, we have removed the sentence in which we raise the possibility of “silent synapses” in order to avoid confusion. The reviewer is also correct that VM7 PNs have inputs from non-ORN presynaptic partners, including LNs and PNs. So again, perhaps increased inhibitory inputs contributes to the near-complete silencing of the PNs. Given the heterogeneity of LN populations, we view this area as fertile ground for future research. 

Language / Data Considerations:

(1) Or42a OSNs have other inputs, namely, from LNs. What are they doing here? Are they also affected?

As discussed above, the question of how LN innervation of Or42a OSNs is altered by critical-period EB exposure is an intriguing one that fully deserves its own follow-up study, and we have tried to avoid speculation about the role of LNs when discussing our pruning phenotype. We note at multiple points throughout the text the importance of LNs and refer to previous studies of LN plasticity in response to chronic odorant exposure. 

(2) In all of the measurements, what happens to synaptic density? Is it maintained? Does it scale precisely? This would be helpful to know.

We have performed the analysis as requested, which is now included in a supplement to Figure 5. We found that synaptic density shows no trend in variation across conditions and glial driver genotypes.

(3) In Figure 5, the controls for the alrm-GAL4 experiments show a much more drastic phenotype than controls in previous figures? Does this background influence how we can interpret the results? Could the response have instead hit a floor effect and it's just not possible to recover?

The reviewer is correct that following EB exposure, astrocyte vs. ensheathing glial driver backgrounds displayed modest differences in the extent of pruning by volume (0.27 for astros, 0.36 for EG). We note that the two drpr RNAi lines that we used had non-significant (but opposite) effects on the estimated size of OSN42a OSN volume in combination with the astrocyte driver, arguing against a floor effect. In addition, a recent publication by Nelson et al. (2024) replicated our findings with a different astrocyte GAL4 driver and draper RNAi line. Thus, we are confident that this result is biologically meaningful and not an artifact of genetic background. 

(4) The estimation of infiltration measurement in Figure 6 is tricky to interpret. It implies that the projections occupy the same space, which cannot be possible. I'd advocate a tempering of some of this language and consider an intensity measurement in addition to their current volume measurements (or perhaps an "occupied space" measurement) to more accurately assess the level of resolution that can be obtained via these methods.

We completely agree that our language in describing EG infiltration could have been more precise, and we modified our language as suggested. The combination of the Or42a-mCD8::GFP label we and others use, our use of confocal microscopy, and our Surface pipeline in Imaris combine to create a glomerular mask that traces the outline of the OSN terminal arbor, but is nonetheless not 100% “filled” by neuronal membrane and/or glial processes. 

(5) Do the authors have the kind of resolution needed to tell whether there is indeed Or42a-positive axon fragmentation (as asserted on p16 and from their data in figures 4, 5, 7). If the authors want to say this, I would advocate for a measurement of fragmentation / total volume to prove it - if not, I would advocate tempering of the current language.

The reviewer brings up a fair criticism: while our assertion about axon fragmentation was based on our visual observations of hundreds of EB-exposed brains, the resolution limits of confocal microscopy do not allow us to rigorously rule out fragmentation within a bundle of OSN axons. Instead, our most compelling evidence for the lack of EB-induced Or42a OSN fragmentation in the absence of glial Draper comes from our new electrophysiology data (Figure 4F-J) in repo-GAL4>UAS-draper RNAi animals. We found no difference in spontaneous release from Or42a terminals in flies exposed to mineral oil or 15% EB from 0-2 DPE, which would not be the case if there was Draper-independent fragmentation along the axons or terminal arbors upon EB exposure. We have updated our discussion of fragmentation so that our statements are based on this new evidence, and not confocal microscopy. 

(6) There is an interesting Discussion opportunity missed here. Some experiments would, ostensibly, require pupae to detect odorants within the casing via structures consistently in place for olfaction during pupation. It would be useful for the authors to discuss a little more deeply when this critical period may arise and why the experiment where pupae are exposed to EB two days before eclosion and there is no response, occurs as it does. I agree that it's clearly a time when they are not sensitive to the odorant, but that could just be because there's no ability to detect odorants at that time. Is it a question of non-sensitivity to EB or just non-sensitivity to everything?

We share the reviewer’s interest in the plasticity of the olfactory circuit during pupariation, although, as they correctly point out, it is difficult to conceive of an odorant-exposure experiment that could disentangle the barrier effects of puparium from the sensitivity of the circuit itself, and our pre-eclosion data in Figure 3A, D, G does not distinguish between the two. While an investigation into mechanism by which the critical period for ethyl butyrate exposure opens and closes is outside the scope of the present study, we would consider the physical barrier of the puparium to be a satisfactory explanation for why eclosion marks the functional opening of experiencedependent plasticity. As the reviewer suggests, we have added this important nuance to our discussion of the opening of the critical period in the corresponding paragraph of the Results, as well as to the Discussion section “Glomeruli exhibit dichotomous responses to critical period odor exposure.” 

Minor Elements:

(1) Page 6 bottom: "Or4a-mCD8::GFP" should be "Or42a-mCD8::GFP"

(2) Page 15, end of last full paragraph. Remove the "e"

Thank you for pointing out these typos. They have been corrected. 

Reviewer #2 (Public Review):

Sensory experiences during developmental critical periods have long-lasting impacts on neural circuit function and behavior. However, the underlying molecular and cellular mechanisms that drive these enduring changes are not fully understood. In Drosophila, the antennal lobe is composed of synapses between olfactory sensory neurons (OSNs) and projection neurons (PNs), arranged into distinct glomeruli. Many of these glomeruli show structural plasticity in response to early-life odor exposure, reflecting the sensitivity of the olfactory circuitry to early sensory experiences.

In their study, the authors explored the role of glia in the development of the antennal lobe in young adult flies, proposing that glial cells might also play a role in experiencedependent plasticity. They identified a critical period during which both structural and functional plasticity of OSN-PN synapses occur within the ethyl butyrate (EB)responsive VM7 glomerulus. When flies were exposed to EB within the first two days post-eclosion, significant reductions in glomerular volume, presynaptic terminal numbers, and postsynaptic activity were observed. The study further highlights the importance of the highly conserved engulfment receptor Draper in facilitating this critical period plasticity. The authors demonstrated that, in response to EB exposure during this developmental window, ensheathing glia increase Draper expression, infiltrate the VM7 glomerulus, and actively phagocytose OSN presynaptic terminals. This synapse pruning has lasting effects on circuit function, leading to persistent decreases in both OSN-PN synapse numbers and spontaneous PN activity as analyzed by perforated patch-clamp electrophysiology to record spontaneous activity from PNs postsynaptic to Or42a OSNs.

In my view, this is an intriguing and potentially valuable set of data. However, since I am not an expert in critical periods or habituation, I do not feel entirely qualified to assess the full significance or the novelty of their findings, particularly in relation to existing research.

We thank the reviewer for their insightful critique of our work. In response to their comments, we added additional physiological analysis and tempered our language around possible explanations for the apparent disconnect between the physiological and morphological critical period odor exposure. These changes are explained in more detail in the response to the public review by Reviewer 1 and also in our responses outlined below. 

Reviewer #2 (Recommendations For The Authors):

I though do have specific comments and questions concerning the presynaptic phenotype they deduce from confocal BRP stainings and electrophysiology.

Concerning the number of active zones: this can hardly be deduced from standardresolution confocal images and, maybe more importantly, lacking postsynaptic markers. This particularly also in the light of them speculating about "silent synapses". There are now tools existing concerning labeled, cell type specific expression of acetylcholine-receptor expression and cholinergic postsynaptic density markers (importantly Drep2). Such markers should be entailed in their analysis. They should refer to previous concerning "brp-short" concerning its original invention and prior usage.

We thank the reviewer for their thoughtful approach to our methodology and claims. While the use of confocal microscopy of Bruchpilot puncta to estimate numbers of presynapses is standard practice (see Furusawa et al., 2023; Aimino et al., 2022; Urwyler et al., 2019; Ackerman et al., 2021), the reviewer is correct that a punctum does not an active zone make. Bruchpilot staining and quantification is a well-validated tool for approximating the number of presynaptic active zones, not a substitute for super-resolution microscopy. We made changes to our language about active zones to make this distinction clearer. We have also removed the sentence where we discuss the possibility of “silent synapses,” which both reviewers felt was too speculative for our existing data. Finally, we are highly interested in characterizing the response of PNs and higher-order processing centers to critical-period odorant exposure as a future direction for our research. However, given the complexity of the subject, we chose to limit the scope of this study to the interactions between OSNs and glia. 

Regarding their electrophysiological analysis and the plausibility of their findings: I am uncertain whether the moderate reduction in BRP puncta at the relevant OSN::PN synapse can fully account for the significantly reduced spontaneous PN activity they report. This seems particularly doubtful in the absence of any direct evidence for postsynaptically silent synapses. Perhaps this is my own naivety, but I wonder why they did not use antennal nerve stimulation in their experiments?

We refer to previous studies of the AL indicating that moderate changes in glomerular volume and presynaptic content can translate to far more striking alterations in electrophysiology and behavior (Devaud et al., 2003; Devaud et al., 2001; Acebes et al., 2012; and Chodankar et al., 2020, Mosca et al., 2017). This literature has demonstrated that chronic odorant exposure can result in remodeling of inhibitory local interneurons to suppress over-active inputs from OSNs. While we do not address the complex subject of interneuron remodeling in the present study, we find it highly likely that there would be significant changes in interneuron innervation of PNs, independent of glial phagocytosis of OSN excitatory inputs, resulting in additional inhibition. Moving forward, we are very interested in expanding these studies to include odor-evoked changes in PN activity.  

Additional minor point: The phrase "Soon after its molecular biology was described (et al., 1999), the Drosophila melanogaster" seems somewhat misleading. Isn't the field still actively describing the molecular biology of the fly olfactory system?

We completely agree and have removed this sentence entirely.  

Reviewing Editor's Note: to enhance the evidence from mostly compelling in most facets to solid would be to add physiology to the Draper analysis.

These experiments have been completed and are presented in Figure 4F-J. 

References

Acebes A, Devaud J-M, Arnés M, Ferrús A. 2012. Central Adaptation to Odorants Depends on PI3K Levels in Local Interneurons of the Antennal Lobe. J Neurosci 32:417–422. doi:10.1523/jneurosci.2921-11.2012

Ackerman SD, Perez-Catalan NA, Freeman MR, Doe CQ. 2021. Astrocytes close a motor circuit critical period. Nature592:414–420. doi:10.1038/s41586-021-03441-2

Aimino MA, DePew AT, Restrepo L, Mosca TJ. 2022. Synaptic Development in Diverse Olfactory Neuron Classes Uses Distinct Temporal and Activity-Related Programs. J Neurosci 43:28–55. doi:10.1523/jneurosci.0884-22.2022

Chodankar A, Sadanandappa MK, VijayRaghavan K, Ramaswami M. 2020. Glomerulus-Selective Regulation of a Critical Period for Interneuron Plasticity in the Drosophila Antennal Lobe. J Neurosci 40:5549–5560. doi:10.1523/jneurosci.2192-19.2020

Das S, Sadanandappa MK, Dervan A, Larkin A, Lee JA, Sudhakaran IP, Priya R, Heidari R, Holohan EE, Pimentel A, Gandhi A, Ito K, Sanyal S, Wang JW, Rodrigues V, Ramaswami M. 2011. Plasticity of local GABAergic interneurons drives olfactory habituation. Proc Natl Acad Sci 108:E646–E654. doi:10.1073/pnas.1106411108 Devaud J, Acebes A, Ramaswami M, Ferrús A. 2003. Structural and functional changes in the olfactory pathway of adult Drosophila take place at a critical age. J Neurobiol 56:13–23. doi:10.1002/neu.10215

Devaud J-M, Acebes A, Ferrus A. 2001. Odor Exposure Causes Central Adaptation and ́Morphological Changes in Selected Olfactory Glomeruli in Drosophila. J Neurosci 21:6274–6282. doi:10.1523/jneurosci.21-16-06274.2001

Furusawa K, Ishii K, Tsuji M, Tokumitsu N, Hasegawa E, Emoto K. 2023. Presynaptic Ube3a E3 ligase promotes synapse elimination through down-regulation of BMP signaling. Science 381:1197–1205. doi:10.1126/science.ade8978

Mosca TJ, Luginbuhl DJ, Wang IE, Luo L. 2017. Presynaptic LRP4 promotes synapse number and function of excitatory CNS neurons. eLife 6:e27347. doi:10.7554/elife.27347

Nelson N, Vita DJ, Broadie K. 2024. Experience-dependent glial pruning of synaptic glomeruli during the critical period. Sci Rep 14:9110. doi:10.1038/s41598-024-59942-3

Urwyler O, Izadifar A, Vandenbogaerde S, Sachse S, Misbaer A, Schmucker D. 2019. Branch-restricted localization of phosphatase Prl-1 specifies axonal synaptogenesis domains. Science 364. doi:10.1126/science.aau9952

Wilson RI, Laurent G. 2005. Role of GABAergic Inhibition in Shaping Odor-Evoked Spatiotemporal Patterns in the Drosophila Antennal Lobe. J Neurosci 25:9069–9079.

doi:10.1523/jneurosci.2070-05.2005

Author response:

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

Reviewer #1 (Public Review): 

Summary:

The goal of this project is to test the hypothesis that individual differences in experience with multiple languages relate to differences in brain structure, specifically in the transverse temporal gyrus. The approach used here is to focus specifically on the phonological inventories of these languages, looking at the overall size of the phonological inventory as well as the acoustic and articulatory diversity of the cumulative phonological inventory in people who speak one or more languages. The authors find that the thickness of the transverse temporal gyrus (either the primary TTG, in those with one TTG, or in the second TTG, in people with multiple gyri) was related to language experience, and that accounting for the phonological diversity of those languages improved the model fit. Taken together, the evidence suggests that learning more phonemes (which is more likely if one speaks more than one language) leads to experience-related plasticity in brain regions implicated in early auditory processing.

Strengths:

This project is rigorous in its approach--not only using a large sample, but replicating the primary finding in a smaller, independent sample. Language diversity is difficult to quantify, and likely to be qualitatively and quantitatively distinct across different populations, and the authors use a custom measure of multilingualism (accounting for both number of languages as well as age of acquisition) and three measures of phonological diversity. The team has been careful in discussion of these findings, and while it is possible that pre-existing differences in brain structure could lead to an aptitude difference which could drive one to learn more than one language, the fine-grained relationships with phonological diversity seem less likely to emerge from aptitude rather than experience. 

Weaknesses:

It is a bit unclear how the measures of phonological diversity relate to one another--they are partially separable, but rest on the same underlying data (the phonemes in each language). It would be helpful for the reader to understand how these measures are distributed (perhaps in a new figure), and the degree to which they are correlated with one another. 

Thank you for the comment. Indeed our description missed this important detail that we now included in the manuscript. Unsurprisingly, the distances all correlated with one another, which we present in Table 2 in Section 2.3 of the revised manuscript. We have also added a figure with distributions of the three distance measures (see Figure S3).

Further, as the authors acknowledge, it is always possible that an unseen factor instead drives these findings--if typological lexical distance measures are available, it would be helpful to enter these into the model to confirm that phonological factors are the specific driver of TTG differences and not language diversity in a more general sense. That said, the relationship between phonological diversity and TTG structure is intuitive. 

Thank you for the suggestion. To further establish that our results reflected the relationship between TTG structure and phonological diversity specifically (as opposed to language diversity in a more general sense), we derived a fourth measure of language experience, where the AoA index of different languages was weighted by lexical distances between the languages. Here, we followed the methodology described in Kepinska, Caballero, et al. (2023): We used Levenshtein Distance Normalized Divided (LDND) (Wichmann et al., 2010) which was computed using the ASJP.R program by Wichmann (https://github.com/Sokiwi/InteractiveASJP01). Information on lexical distances was combined with language experience information per participant using Rao's quadratic entropy equation in the same way as for the phonological measures.

We then entered this language experience measure accounting for lexical distances between the languages into linear models predicting the thickness of the second left and right TTG (controlling for participants’ age, sex and mean hemispheric thickness) in the main sample, and compared these models with the corresponding models including the original three phonological distance measures (models 24 in Author response table 1), and the measure with no typological information (1).

Below, we list adjusted R2 values of all models, from which it is clear that the index of multilingual language experience accounting for lexical distances between languages (5) explained less variance than the index incorporating phoneme-level distances between languages (2), both in the left and the right hemisphere. This further strengthens our conclusion that our results reflected the relationship between TTG structure and phonological diversity specifically, as opposed to language diversity in a more general sense.

Author response table 1.

We have added a description of this analysis to the manuscript, Section 3.3, lines 357-370.

One curious aspect of this paper relates to the much higher prevalence of split or duplicate TTG in the sample. The authors do a good job speculating on how features of the TASH package might lead to this, but it is unclear where the ground truth lies--some discussion of validation of TASH against a gold standard would be useful. 

The validation of the TASH toolbox in comparison to gold standard manual measurement involved assessing how well the measurements of left and right Heschl's gyrus (HG) volumes obtained using the TASH method correlated with those obtained through manual labeling (see Dalboni da Rocha et al., 2020 for details). This validation process was conducted across three independent datasets. Additionally, for comparison, the manually labeled HG volumes were also compared with those obtained using FreeSurfer's Destrieux parcellation of the transverse temporal gyrus in the same datasets. The validation process, therefore, involved rigorous comparisons of HG volumes obtained through manual labeling, FreeSurfer, and TASH across different datasets, along with an assessment of inter-rater reliability for the manual labeling procedure. This comprehensive approach ensures that the results are robust and reliable. TASH_complete, the version used in the present work, is an extension of the extensively validated TASH, which apart from the first gyrus, also identifies additional transverse temporal gyri (i.e. Heschl’s gyrus duplications and multiplications) situated in the PT, when present. Since work on the correspondence between manually identified TTG multiplications is still ongoing, as outlined in the Methods section, we complemented the automatic segmentation by extensive visual assessment of the identified posterior gyri. This process involved removing from the analysis those gyri that lay along the portion of the superior temporal plane that curved vertically (i.e., within the parietal extension, Honeycutt et al., 2000), when present. Given that TASH_complete and TASH operate on the same principles and are both based on FreeSurfer’s surface reconstruction and cortical parcellation (which have been extensively validated against manual tracing and other imaging modalities, showing good accuracy), and since we have visually inspected all segmentations, we are confident as to the accuracy of the reported TTG variability. It has to be further noted that the prevalence of TTG multiplications beyond 2nd full posterior duplications was not systematically assessed in previous descriptive reports (Marie, 2015). However, we acknowledge that more work is needed to further ascertain anatomical accuracy of the segmentations, and we elaborate on this point in the Discussion of the revised manuscript (lines 621-623).

Reviewer #2 (Public Review):

This work investigates the possible association between language experience and morphology of the superior temporal cortex, a part of the brain responsible for the processing of auditory stimuli. Previous studies have found associations between language and music proficiency as well as language learning aptitude and cortical morphometric measures in regions in the primary and associated auditory cortex. These studies have most often, however, focused on finding neuroanatomical effects of difference between features in a few (often two) languages or from learning single phonetic/phonological features and have often been limited in terms of N. On this background, the authors use more sophisticated measures of language experience that take into account the age of onset and the differences in phonology between languages the subjects have been exposed to as well as a larger number of subjects (N = 146 + 69) to relate language experience to the shape and structure of the superior temporal cortex, measured from T1weighted MRI data. It shows solid evidence for there being a negative relationship between language experience and the right 2nd transverse temporal gyrus as well as some evidence for the relationship representing phoneme-level cross-linguistic information. 

Strengths 

The use of entropy measures to quantify language experience and include typological distance measures allows for a more general interpretation of the results and is an important step toward respecting and making use of linguistic diversity in neurolinguistic experiments. 

A relatively large group of subjects with a range of linguistic backgrounds. 

The full analysis of the structure of the superior temporal cortex including cortical volume, area, as well as the shape of the transverse gyrus/gyri. There is a growing literature on the meaning of the shape and number of the transverse gyri in relation to language proficiency and the authors explore all measures given the available data. 

The authors chose to use a replication data set to verify their data, which is applaudable. However, see the relevant point under "Weaknesses". 

Weaknesses 

The authors fail to explain how a thinner cortex could reflect the specialization of the auditory cortex in the processing of diverse speech input. The Dynamic Restructuring Model (Pliatsikas, 2020) which is referred to does not offer clear guidance to interpretation. A more detailed discussion of how a phonologically diverse environment could lead to a thinner cortex would be very helpful. 

Thank you for bringing our attention to this point. We have now extended the explanation we had previously included in the Discussion by including the following passage on p. 20 (lines 557-566) of the revised manuscript:

“Experience-induced pruning is essential for maintaining an efficient and adaptive neural network. It reinforces relevant neural circuits for faster more efficient information processing, while diminishing those that are less active, or less beneficial. The cortical specialization may need to arise because phonologically more diverse language experience requires that the mapping of acoustic signal to sound categories is denser, more detailed and more intricate. As a result, the brain may need to engage in more intensive processing to discriminate between and accurately perceive the sound categories of each language. This increased cognitive demand may, in turn, require the auditory and language processing regions of the brain to adapt and become more efficient. Over time, this heightened effort for successful speech perception and sound discrimination may lead to neural plasticity, resulting in cortical specialization. This means that cortical areas become more finely tuned and specialized for processing the unique phonological features of language(s) spoken by individuals.” 

We have also added a passage to the Introduction regarding the possible microscopic or physiological underpinnings of the brain structural differences that we observe macroscopically using structural MRI (lines 68-73): 

“Such environmental effect on cortical thickness might in turn be tied to microstructural changes to the underlying brain tissue, such as modifications in dendritic length and branching, synaptogenesis or synaptic pruning, growth of capillaries and glia, all previously tied to some kind of environmental enrichment and/or skill learning (see Lövdén et al., 2013; Zatorre et al., 2012 for overviews). Increased cortical thickness may reflect synaptogenesis and dendritic growth, while cortical thinning observed with MRI may be a result of increased myelination (Natu et al., 2019) or synaptic pruning.”

It is difficult to understand what measure of language experience is used when. Clearer and more explicit nomenclature would assist in the interpretation of the results. 

We have added more explicit list of indices used in the Introduction (lines 104-107 of the revised manuscript) and in Section 2.4 and used them consistently throughout the text:

(1) language experience index not accounting for typological features: ‘Language experience - no typology’

(2) measures combining language experience with typological distances at different levels: 

a. ‘Language experience – features’, 

b. ‘Language experience – phonemes’, 

c. ‘Language experience – phonological classes’.

There is a lack of description of the language backgrounds of the included subjects. How many came from each of the possible linguistic backgrounds? How did they differ in language exposure? This would be informative to evaluate the generalizability of the conclusions. 

Thank you for raising this point. Given the complexity of participants’ language experience, ranging between monolingual to speaking 7 different languages, we opted for a fully parametric approach in quantifying it. We used the Shannon’s entropy and Rao’s quadratic entropy equations to create continuous measures of language experience, without the constraints of a minimum sample size per language and the need to exclude participants with underrepresented languages. To add further details in our description of the language background, we summarize the language background of both samples in the newly added Table 1 presenting a breakdown of participants by number of languages they spoke, and Supplementary Table S1 listing all languages spoken by each participant.

Only the result from the multiple transverse temporal gyri (2nd TTG) is analyzed in the replicated dataset. Only the association in the right hemisphere 2nd TTG is replicated but this is not reflected in the discussion or the conclusions. The positive correlation in the right TTG is thus not attempted to be replicated. 

Thank you for bringing this point to our attention. Since only few participants presented single gyri in the left (n = 7) and the right hemisphere (n = 14), the replication analysis focused on the second TTG results only. We have now commented on this fact in Section 3.5 (lines 413-415), as well as in the Discussion (lines 594-596). 

The replication dataset differed in more ways than the more frequent combination of English and German experience, as mentioned in the discussion. Specifically, the fraction of monolinguals was higher in the replication dataset and the samples came from different scanners. It would be better if the primary and replication datasets were more equally matched. 

Indeed, the replication sample did not fully mimic the characteristics of the main sample and a better match between the two samples would have been preferable. As elaborated in the Introduction, however, the data was split into two groups according to the date of data acquisition, which also coincided with the field strength of the scanners used for data acquisition: the first, main sample’s data were acquired on a 1.5T, the replication sample’s on 3T. We opted for keeping this split and not introducing additional noise in the analysis by using data from different field strengths at the cost of not fully matching the two datasets. Observing the established effects (even partially) in this somewhat different replication sample, however, seems in our view to further strengthen our results. 

Even if the language experience and typological distance measures are a step in the right direction for correctly associating language exposure with cortical plasticity, it still is a measure that is insensitive to the intensity of the exposure. The consequences of this are not discussed. 

Indeed, we agree with the reviewer that there is still a lot of grounds to cover to fully understand the relationship between language experience and cortical plasticity. We have added a paragraph to the Discussion (lines 587-592 of the revised manuscript) to bring attention to this issue:

“Future research should also further increase the degree of detail in describing the multilingual language experience, as both AoA and proficiency (used here) are not sensitive to other aspects of multilingualism, such as intensity of the exposure to the different languages, or quantity and quality of language input. Since these aspects have been convincingly shown to be associated with neural changes (e.g., Romeo, 2019), incorporating further, more detailed measures describing individuals’ language experience could further enhance our understanding of cortical plasticity in general, and how the brain accommodates variable language experience in particular.” 

Reviewer #3 (Public Review): 

Summary: 

The study uses structural MRI to identify how the number, degree of experience, and phonemic diversity of language(s) that a speaker knows can influence the thickness of different sub-segments of the auditory cortex. In both a primary and replication sample of adult speakers, the authors find key differences in cortical thickness within specific subregions of the cortex due to either the age at which languages are acquired (degree of experience), or the diversity of the phoneme inventories carried by that/those language(s) (breadth of experience). 

Strengths: 

The results are first and foremost quite fascinating and I do think they make a compelling case for the different ways in which linguistic experience shapes the auditory cortex. 

The study uses a number of different measures to quantify linguistic experience, related to how many languages a person knows (taking into account the age at which each was learned) as well as the diversity of the phoneme inventories contained within those languages. The primary sample is moderately large for a study that focuses on brainbehaviour relationships; a somewhat smaller replication sample is also deployed in order to test the generality of the effects. 

Analytic approaches benefit from the careful use of brain segmentation techniques that nicely capture key landmarks and account for vagaries in the structure of STG that can vary across individuals (e.g., the number of transverse temporal gyri varies from 1-4 across individuals). 

Weaknesses: 

The specificity of these effects is interesting; some effects really do appear to be localized to the left hemisphere and specific subregions of the auditory cortex e.g., TTG. However because analyses only focus on auditory regions along the STG and MTG, one could be led to the conclusion that these are the only brain regions for which such effects will occur. The hypothesis is that these are specifically auditory effects, but that does make a clear prediction that nonauditory regions should not show the same sort of variability. I recognize that expanding the search space will inflate type-1 errors to a point where maybe it's impossible to know what effects are genuine. And the fine-grained nature of the effects suggests a coarse analysis of other cortical regions is likely to fail. So I don't know the right answer here. Only that I tend to wonder if some control region(s) might have been useful for understanding whether such effects truly are limited to the auditory cortex. Otherwise one might argue these are epiphenomenal or some hidden factor unrelated to auditory experience predicting that we'd also see them in the non-auditory cortex as well, either within or outside the brain's speech network(s). 

Thank you for raising this important issue. Our primary analyses indeed focused on the auditory regions, given their involvement in speech and language processing at different levels of processing hierarchy (from low – HG, to high – STG and STS). Here, we included a fairly broad range of ROIs (8 per hemisphere, 16 in total) and it has to be noted that it was only the bilateral planum temporale which showed an association with multilingualism. In the original submission we had indeed attempted at confirming the specificity of this result by performing a whole-brain vertex-wise analysis in freesurfer (see Table 3, Section 3.2, Figure S5), which again showed that the only cluster of vertices related to participants’ language experience at p < .0001 (uncorrected) was located in the superior aspect of the left STG, corresponding to the location of planum temporale and the second TTG. Lowering the threshold of statistical significance to p < .001 (uncorrected) results in further clusters of vertices whose thickness was positively associated with the degree of multilingual language experience localized in:

• Left hemisphere: central sulcus (S_cenral), long insular gyrus and central sulcus of the insula (G_Ins_lg_and_S_cent_ins), lingual gyrus (G_oc-temp_med-Lingual), planum temporale of the superior temporal gyrus (G_temp_sup-Plan_tempo), short insular gyri (G_insular_short), middle temporal gyrus (G_temporal_middle), and planum polare of the superior temporal gyrus (G_temp_sup-Plan_polar)

• Right hemisphere: angular gyrus (G_pariet_inf-Angular), superior temporal sulcus (S_temporal_sup), middle-posterior part of the cingulate gyrus and sulcus (G_and_S_cingul-Mid-Post), marginal branch of the cingulate sulcus (S_cingul-Marginalis), parieto-occipital sulcus (S_parieto_occipital), parahippocampal gyrus (G_oc-temp_med-Parahip), Inferior temporal gyrus (G_temporal_inf)

We present the result of this analysis in Author response image 1, where clusters are labelled according to the Destrieux anatomical atlas implemented in FreeSurfer:

Author response image 1.

As the reviewer points out, establishing relationships between our dependent and independent variables at a lower threshold of statistical significance might not reflect a true effect, and it is statistically more probable that multilingualism-related cortical thickness effects seem to be specific to the auditory regions. We do not exclude that an analysis of other pre-defined ROIs, performed at a similar level of detail as our present investigation, would uncover further significant associations between multilingual language experience and brain anatomy, but such an investigation is beyond the scope of the present work.

The reason(s) why we might find a link between cortical thickness and experience is not fully discussed. The introduction doesn't really mention why we'd expect cortical thickness to be correlated (positively or negatively) with speech experience. There is some discussion of it in the Discussion section as it relates to the Pliatsikas' Dynamic Restructuring Model, though I think that model only directly predicts thinning as a function of experience (here, negative correlations). It might have less to say about observed positive correlations e.g., HG in the right hemisphere. In any case, I do think that it's interesting to find some relationship between brain morphology and experience but clearer explanations for why these occur could help, and especially some mention of it in the intro so readers are clearer on why cortical thickness is a useful measure. 

We have expanded the section of the Introduction introducing cortical thickness pointing to different microstructural changes previously associated with environmental enrichment and skill learning (lines 68-73), and hope the link between cortical thickness and multilingual language experience is clearer now:

“Such environmental effect on cortical thickness might in turn be tied to microstructural changes to the underlying brain tissue, such as modifications in dendritic length and branching, synaptogenesis or synaptic pruning, growth of capillaries and glia, all previously tied to some kind of environmental enrichment and/or skill learning (see Lövdén et al., 2013; Zatorre et al., 2012 for overviews). Increased cortical thickness may reflect synaptogenesis and dendritic growth, while cortical thinning observed with MRI may be a result of increased myelination (Natu et al., 2019) or synaptic pruning.”

In addition, we have also expanded the Discussion section providing more reasoning for the links between cortical thickness and multilingual language experience (lines 557-566):

“Experience-induced pruning is essential for maintaining an efficient and adaptive neural network. It reinforces relevant neural circuits for faster more efficient information processing, while diminishing those that are less active, or less beneficial. The cortical specialization may need to arise because phonologically more diverse language experience requires that the mapping of acoustic signal to sound categories is denser, more detailed and more intricate. As a result, the brain may need to engage in more intensive processing to discriminate between and accurately perceive the sound categories of each language. This increased cognitive demand may, in turn, require the auditory and language processing regions of the brain to adapt and become more efficient. Over time, this heightened effort for successful speech perception and sound discrimination may lead to neural plasticity, resulting in cortical specialization. This means that cortical areas become more finely tuned and specialized for processing the unique phonological features of language(s) spoken by individuals.” 

One pitfall of quantifying phoneme overlap across languages is that what we might call a single 'phoneme', shared across languages, will, in reality, be realized differently across them. For instance, English and French may be argued to both use the vowel /u/ although it's realized differently in English vs. French (it's often fronted and diphthongized in many English speaker groups). Maybe the phonetic dictionaries used in this study capture this using a close phonetic transcription, but it's hard to tell; I suspect they don't, and in that case, the diversity measures would be an underestimate of the actual number of unique phonemes that a listener needs to maintain. 

The PHOIBLE database uses transcription that reflects phonological descriptive data as closely as possible, according to the available descriptive sources. Different realizations of sounds are (as much as possible) marked in the database. For example, the open front unrounded vowel /a/ is listed as e.g., [a] or [a̟ ], with the “+” sign denoting a fronted realization. This is done in PHOIBLE by the use of diacritics (see https://phoible.org/conventions) which further specify variations on the language-specific realizations of the phonemes listed in the database. Further details are available in Moran (2012) (https://digital.lib.washington.edu/researchworks/items/0d26e54d-950a-4d0b-b72c-3afb4b1aa9eb). In our calculation of phoneme-based distances a sign with and without a diacritic were treated as different phonemes, and therefore the different realizations were accounted for.

That said, we fully agree with the reviewer that in fact any diversity measure will be an underestimation of the actual variation, as between-speaker micro-variation can never be fully reflected in largescale typological databases as the one used in the present study. To the best of our knowledge, however, PHOIBLE offers the most comprehensive way of allowing for quantifying cross-linguistic variation to date, and we are looking forward for the field to offer further tools capturing the linguistic variability at an ever-finer level of detail. 

Discussion of potential genetic differences underlying the findings is interesting. One additional data point here is a study finding a relationship between the number of repeats of the READ1 (a factor of the DCDC2 gene) in populations of speakers, and the phoneme inventory of language(s) predominant in that population (DeMille, M. M., Tang, K., Mehta, C. M., Geissler, C., Malins, J. G., Powers, N. R., ... & Gruen, J. R. (2018). Worldwide distribution of the DCDC2 READ1 regulatory element and its relationship with phoneme variation across languages. Proceedings of the National Academy of Sciences, 115(19), 4951-4956.) Admittedly, that paper makes no claim about the cortical expression of that regulatory factor under study, and so more work needs to be done on whether this has any bearing at all on the auditory cortex. But it does represent one alternative account that does not have to do with plasticity/experience. 

We thank the reviewer for bringing this important line of research to our attention, which we now included in the Discussion (lines 494-498 of the revised manuscript).

The replication sample is useful and a great idea. It does however feature roughly half the number of participants meaning statistical power is weaker. Using information from the first sample, the authors might wish to do a post-hoc power analysis that shows the minimum sample size needed to replicate their effect; given small effects in some cases, we might not be surprised that the replication was only partial. I don't think this is a deal breaker as much as it's a way to better understand whether the failure to replicate is an issue of power versus fragile effects. 

Thank you for the suggestion. Indeed, the effect sizes established in the analyses using the main sample were small (e.g., f2 = 0.07). According to a power analysis performed with G*Power 3.1 (Faul et al., 2009), detecting an effect of this magnitude of the predictor of interest at alpha = .05 (two-tailed), in a linear multiple regression model with 4 predictors (i.e., 3 covariates of no-interest: sex, age, hemispheric thickness, and 1 predictor of interest), a sample of N = 114 is required to achieve 80% of power. Our partial lack of replicating the effect might therefore indeed be related to a lower power of the replication sample, rather than the effect itself being fragile.

Recommendations for the authors:

Reviewer #1 (Recommendations for the Authors): 

A few remaining details that I think you can handle: 

(1) Was there any correction for multiple comparisons, especially when multiple anatomical measures were investigated in separate models? (e.g. ln 130). 

Since three different anatomical measures were investigated in Analysis 1 and Analysis 2 (see Table 1), the alpha level of the two linear mixed models was lowered to α = .0166. Note that the p-values of the predictors of interest were p = .012 (mixed model with all auditory regions) and p = .005 (mixed model with all identified TTGs).

(2) In Table 2, since your sample skews heavily female, it would be more useful to present the counts of Male/Female totals for 1, 2, 3, 4, etc TTGs as proportions of the total for that sex rather than counts, so that the distribution across sex is more obvious. 

Thank you for bringing this issue to our attention. We have now included an additional row in Table 4, with proportions of males and females presenting different total number of identified gyri in the left and the right hemisphere.

(3) (ln 161) It wasn't clear to me how you dealt statistically with the fact that some participants had only one TTG - did you simply enter "0" as a value for cortical thickness for 2, 3, etc. for those participants? If so, it's possible that this result could reflect the number of split/duplicated gyri rather than the thickness of those gyri. 

Indeed, if non-existing gyri were coded with a value of “0” (it being the lowest possible thickness value), the results would reflect the configuration of TTGs (single vs multiple gyri) rather than a relationship between thickness and language experience.

The model was, however, fit to all available thickness values, and the gyri labels (1st, 2nd, 3rd) were modeled as a fixed factor with 3 levels. This procedure allowed us to localize the effect of language experience to a specific gyrus. The following formula was used with the lmer package in R:

thickness ~ age + sex + whole_brain_thickness + language_experience* gyrus*hemisphere + (1 | participant_id)

We observed a significant interaction between language experience and the 2nd gyrus (NB. no significant 3-way interaction between language experience, the 2nd gyrus and hemisphere pointed to the effect being bilateral). This result was then followed up with two linear models: one for the thickness values of the 2nd left and one for the 2nd right gyrus, each fit to the available data only (n = 130 for the left hemisphere; n = 96 for the right), see Table 5. This procedure ensured that only the available cortical thickness data were considered when establishing their relationship with our independent variable (language experience).

(4) I think more could be done in the results section to distinguish your three phonological measures--these details are evident in the Methods section, but if readers consume this paper front to back they may find it difficult to figure out what each measure really means. 

Thank you. We have added more explicit list of indices used in the Introduction (lines 104-107) and in Section 2.4. As per Reviewer #2 comments, the Methods section was also moved before the Results section, hopefully further enhancing the readability of the paper.

Typos: 

ln 270: "weighed"--could you have meant "weighted"? 

Corrected, thank you! 

ln 377: "Apart from phoneme-based typological distance measure explaining" --> "Apart from *the* phonemebased..." 

Corrected, thank you! 

Reviewer #2 (Recommendations for the Authors): 

The interpretation of the results would be much helped by the methods section being moved to precede it. Now, much of the results section is methods summaries that would not have been needed if the reader had been presented with the methods beforehand. This is especially true for the measures of language experience and typological distances used. 

Thank you. We have moved the Materials and Methods section before the Results section.

The equation in section "4.2 Language experience" should be H = - sum(p_i log2 (p_i)) and not H = - sum(p_i log2(i)). 

Corrected, thank you! 

It is unclear what "S" represents in the equation in the section "4.4 Combining typology and language experience (indexed by AoA)".  

The explanation has been added, thank you!

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Liu et al. present CROWN-seq, a technique that simultaneously identifies transcription-start nucleotides and quantifies N6,2'-O-dimethyladenosine (m6Am) stoichiometry. This method is derived from ReCappable-seq and GLORI, a chemical deamination approach that differentiates A and N6-methylated A. Using ReCappable-seq and CROWN-seq, the authors found that genes frequently utilize multiple transcription start sites, and isoforms beginning with an Am are almost always N6-methylated. These findings are consistently observed across nine cell lines. Unlike prior reports that associated m6Am with mRNA stability and expression, the authors suggest here that m6Am may increase transcription when combined with specific promoter sequences and initiation mechanisms. Additionally, they report intriguing insights on m6Am in snRNA and snoRNA and its regulation by FTO. Overall, the manuscript presents a strong body of work that will significantly advance m6Am research.

Strengths:

The technology development part of the work is exceptionally strong, with thoughtful controls and well-supported conclusions.

We appreciate the reviewer for the very positive assessment of the study. We have addressed the concerns below.

Weaknesses:

Given the high stoichiometry of m6Am, further association with upstream and downstream sequences (or promoter sequences) does not appear to yield strong signals. As such, transcription initiation regulation by m6Am, suggested by the current work, warrants further investigation.

We thank the reviewer for the insightful comments. We have softened the language related to m⁶Am and transcription regulation. We totally agree with the reviewer that future investigation is required to determine the molecular mechanism behind m⁶Am and transcription regulation.

Reviewer #2 (Public review):

Summary:

In the manuscript "Decoding m6Am by simultaneous transcription-start mapping and methylation quantification" Liu and co-workers describe the development and application of CROWN-Seq, a new specialized library preparation and sequencing technique designed to detect the presence of cap-adjacent N6,2'-O-dimethyladenosine (m6Am) with single nucleotide resolution. Such a technique was a key need in the field since prior attempts to get accurate positional or quantitative measurements of m6Am positioning yielded starkly different results and failed to generate a consistent set of targets. As noted in the strengths section below the authors have developed a robust assay that moves the field forward.

Furthermore, their results show that most mRNAs whose transcription start nucleotide (TSN) is an 'A' are in fact m6Am (85%+ for most cell lines). They also show that snRNAs and snoRNAs have a substantially lower prevalence of m6Am TSNs.

Strengths:

Critically, the authors spent substantial time and effort to validate and benchmark the new technique with spike-in standards during development, cross-comparison with prior techniques, and validation of the technique's performance using a genetic PCIF1 knockout. Finally, they assayed nine different cell lines to cross-validate their results. The outcome of their work (a reliable and accurate method to catalog cap-adjacent m6Am) is a particularly notable achievement and is a needed advance for the field.

Weaknesses:

No major concerns were identified by this reviewer.

We thank the reviewer for the positive assessment of the method and dataset. We have addressed the concerns below.

Mid-level Concerns:

(1) In Lines 625 and 626, the authors state that “our data suggest that mRNAs initate (mis-spelled by authors) with either Gm, Cm, Um, or m6Am.” This reviewer took those words to mean that for A-initiated mRNAs, m6Am was the ‘default’ TSN. This contradicts their later premise that promoter sequences play a role in whether m6Am is deposited.

We thank the reviewer for the comment. We have changed this sentence into “Instead, our data suggest that mRNAs initiate with either Gm, Cm, Um, or Am, where Am are mostly m⁶Am modified.” The revised sentence separates the processes of transcription initiation and m⁶Am deposition, which will not confuse the reader.

(2) Further, the following paragraph (lines 633-641) uses fairly definitive language that is unsupported by their data. For example in lines 637 and 638 they state “We found that these differences are often due to the specific TSS motif.” Simply, using ‘due to’ implies a causative relationship between the promoter sequences and m6Am has been demonstrated. The authors do not show causation, rather they demonstrate a correlation between the promoter sequences and an m6Am TSN. Finally, despite claiming a causal relationship, the authors do not put forth any conceptual framework or possible mechanism to explain the link between the promoter sequences and transcripts initiating with an m6Am.

(3) The authors need to soften the language concerning these data and their interpretation to reflect the correlative nature of the data presented to link m6Am and transcription initiation.

For (2) and (3). We have softened the language in the revised manuscript. Specifically, for lines 633-641 in the original manuscript, we have changed “are often due to” into “are often related to” in the revised manuscript, which claims a correlation rather than a causation.

Reviewer #3 (Public review):

Summary:

m6Am is an abundant mRNA modification present on the TSN. Unlike the structurally similar and abundant internal mRNA modification m6A, m6Am’s function has been controversial. One way to resolve controversies surrounding mRNA modification functions has been to develop new ways to better profile said mRNA modification. Here, Liu et al. developed a new method (based on GLORI-seq for m6A-sequencing), for antibody-independent sequencing of m6Am (CROWN-seq). Using appropriate spike-in controls and knockout cell lines, Liu et al. clearly demonstrated CROWN-seq’s precision and quantitative accuracy for profiling transcriptome-wide m6Am. Subsequently, the authors used CROWN-seq to greatly expand the number of known m6Am sites in various cell lines and also determine m6Am stoichiometry to generally be high for most genes. CROWN-seq identified gene promoter motifs that correlate best with high stoichiometry m6Am sites, thereby identifying new determinants of m6Am stoichiometry. CROWN-seq also helped reveal that m6Am does not regulate mRNA stability or translation (as opposed to past reported functions). Rather, m6Am stoichiometry correlates well with transcription levels. Finally, Liu et al. reaffirmed that FTO mainly demethylates m6Am, not of mRNA but of snRNAs and snoRNAs.

Strengths:

This is a well-written manuscript that describes and validates a new m6Am-sequencing method: CROWN-seq as the first m6Am-sequencing method that can both quantify m6Am stoichiometry and profile m6Am at single-base resolution. These advantages facilitated Liu et al. to uncover new potential findings related to m6Am regulation and function. I am confident that CROWN-seq will likely be the gold standard for m6Am-sequencing henceforth.

Weaknesses:

Though the authors have uncovered a potentially new function for m6Am, they need to be clear that without identifying a mechanism, their data might only be demonstrating a correlation between the presence of m6Am and transcriptional regulation rather than causality.

We thank the reviewer for the very positive assessment of the CROWN-seq method. We have softened the language which is related to the correlation between m⁶Am and transcription regulation.

Reviewer recommendations:

We thank the reviewers for their constructive suggestions. In the revised manuscript, we have corrected the errors and updated the requested discussions and figures.

Reviewer #1 (Recommendations for the authors):

(1) The prior work from the research group, "Reversible methylation of m6Am in the 5′ cap controls mRNA stability" (PMID: 28002401), should be cited, even if the current findings differ from earlier conclusions-particularly in line 58 and the section titled "m6Am does not substantially influence mRNA stability or translation".

We thank the reviewer for this comment. We have added the citation.

(2) I wonder why the authors chose to convert A to I before capping and recapping, as RNA fragmentation caused by chemical treatment may introduce noise into these processes.

We thank the reviewer for this comment. This is a very good point. We have indeed considered this alternative protocol. There are two concerns in performing decapping-and-recapping before A-to-I conversion: (1) it is unclear whether the 3’-desthiobiotin, which is essential for the 5’ end enrichment, is stable or not during the harsh A-to-I conversion; (2) performing decapping-and-recapping first requires more enzyme and 3’-desthiobiotin-GTP, which are the major cost of the library preparation. This is because the input of CROWN-seq (~1 μg mRNA) is much higher than that in ReCappable-seq (~5 μg total RNA or ~250 ng mRNA). In the current protocol, many 5’ ends are highly fragmented and therefore are lost during the A-to-I conversion. As a result, less enzyme and 3’-desthiobiotin-GTP are needed.

(3) During CROWN-seq benchmarking, the authors found that 93% of reads mapped to transcription start sites, implying a 7% noise level with a spike-in probe. This noise could lead to false positives in TSN assignments in real samples. It appears that additional filters (e.g., a known TSS within 100 nt) were applied to mitigate false positives. If so, I recommend that the authors clarify these filters in the main text.

We thank the reviewer for this comment. We think that the spike-in probes might lead to an underestimation of the accuracy of TSN mapping. The spike-in probes are made by in vitro transcription with m⁷Gpppm⁶AmG or m⁷GpppAmG analogs. We found that the in vitro transcription exhibits a small amount of non-specific initiation, which leads to spike-in probes with 5’ ends that are not precisely aligned with the desired TSS. To better illustrate the mapping accuracy of CROWN-seq, we provided Figure 2H, which compares the non-conversion rates of newly found A-TSNs between wild-type and PCIF1 knock cells. If the newly found A-TSNs are real, they should show high non-conversion rates in wild-type cells (i.e., high m⁶Am) and almost zero non-conversion rates (i.e., Am) in PCIF1 knockout cells. As expected, most of the newly found A-TSNs are true A-TSNs since they are m6Am in wild-type and Am in PCIF1 knockout. Thus, we think that CROWN-seq is very precise in TSS mapping. We have clarified this in the Discussion.

(4) I wonder if PCIF1 knockout affects TSN choice and abundance. If not, this data should be presented. If so, how are these changes accounted for in Figure 2H and Figure S5?

We thank the reviewer for this comment.  PCIF1 KO does not really affect TSN choice. Here we calculate the correlation of relative TSN expression within genes between wild-type and PCIF1 KO cells (shown using Pearson’s r). It shows that most of the genes have similar TSN choices (with higher Pearson’s r) in both wild-type and PCIF1 KO cells. Thus, PCIF1 KO does not alter global TSN expressions.

Author response image 1.

(5) The manuscript refers to Am as a rare modification in mRNA (e.g., introduction lines 101-102; discussion lines 574, 608; and possibly other locations) without specifying this only applies to transcription start sites. As this study does not cover entire mRNA sequences, these statements may not be misleading.

We thank the reviewer for this comment.  We have clarified it.

Reviewer #2 (Recommendations for the authors):

(1) On line 122, the authors state that: "On average, a gene uses 9.5{plus minus}9 (mean and s.d., hereafter) TSNs (Figure 1A)." However, they do not discuss the dispersion apparent in the TSNs they observed. Figure panels 1A, B, and S1A, B show a range of 120 bases or less. What is the predominant range of distances between annotated TSNs and the newly identified ones?

1a) For example, what percentage of new TSNs fall within 20? 50? 75? bases of the annotated sites? Additional text describing the distribution of these TSNs would help readers better understand the diversity inherent in these novel 5' RNA ends. Notably, this additional text likely is best placed in the CROWN-Seq section related to Figure 2 or S2.

We thank the reviewer for this comment. We have updated Figure S2 to describe the newly found TSSs. Depending on the coverage in CROWN-seq, the TSSs with higher coverage tend to overlap with or locate proximally to known TSSs. In contrast, the TSSs with low coverage tend to be located further away from annotated TSSs.

1b) The alternate TSNs can have effects on splicing patterns and isoform identity. Providing a few sentences to explain how regularly this occurs would be helpful.

We thank the reviewer for this comment. It is a very interesting point. Different TSNs can indeed have different splicing patterns. Although the discovery of splicing patterns regulated by TSNs is out of the scope of this study, we have discussed this possibility in the revised Discussion section.

(2) On Lines 241 and 242, the authors mentioned that 1284 sites were excluded from the analysis based on low (under 20-explained in the figure legend) read count, distance from TSS, or false negatives (which are not explained). Although I agree that the authors are justified in setting these reads aside, the information could be useful to readers willing to perform follow-up work if their mRNAs of interest were included in these 1284 sites.

2a) An annotation of all of these sites (broken down by category, i.e. the 811, the 343, and the 130) as a supplementary table should be provided.

We thank the reviewer for this comment. We have added the categories to the revised Table S1.

(3) Although I have marked several typos/grammar mistakes in several parts of this review, others exist elsewhere in the text and should be corrected.

We thank the reviewer for this comment. We have corrected them.

(4) In lines 122 and 123 the authors say "Only ~9% of genes contain a single TSN (Figure 1A)." However, their figure shows 81% with a single TSN. Why is there a 10% discrepancy?

We thank the reviewer for this comment. We have corrected the plot in Figure 1A, to match the description.

(5) The first Tab of Table S2 is labeled 'Legend', but is blank. Is this intentional?

We thank the reviewer for this comment. We have updated the table legends.

(6) On lines 70 and 76 of the supplementary figure file pertaining to Figure S2, the legend labels for Figure S2E and S2F are not accurate, they need to be changed to G and H.

(7) In Figure 4A 'percentile' is misspelled.

(8) The color-coding legend for the 4 bases is missing from (and should be added to) Figure S4A.

(9) On Lines 984, 1163, and 1194 the '2s' should be properly sub-scripted where appropriate.

For (6) to (9). We thank the reviewer for finding these issues. We have now corrected them.

Reviewer #3 (Recommendations for the authors):

(1) The authors should discuss if their results can definitively distinguish between the SSCA+1GC motif promoting m6Am that, in turn, promotes transcription, versus the SCA+1GC motif promoting m6Am but also separately promoting transcription in a m6Am-independent manner. The authors should also discuss this in light of recent findings by An et al. (2024 Mol. Cell), which support the former conclusion.

We thank the reviewer for the suggestion. We now have updated the Discussion to address that our paper and An et al. can support each other.

(2) Given that the authors showed m6Am promotes gene expression (Figure 5) but does not affect mRNA stability (Fig. S5), logic dictates that m6Am must regulate mRNA transcription. However, the authors should explain why this regulation focuses on the initiation aspect of transcription rather than other aspects of transcriptional e.g. premature termination, pause release, and elongation.

We thank the reviewer for this comment. In this study, we did not profile the 3’ ends of nascent RNAs and thus we can only make conclusions about the overall transcription process but not a specific aspect. We have updated the revised Discussion section to mention that An et al. discovered that m⁶Am can sequester PCF11 and thus promote transcription, and therefore some of the effects we see could be related to differential premature termination.

(3) Authors should add alternative versions of Figure 1D but with 3 colours corresponding to Am vs. m6Am vs. Cm/Gm/Um for all the cells, they performed CROWN-seq on.

We thank the reviewer for this comment. We have updated Figure S5 as the corresponding figure showing the fraction of Am vs. m6Am vs. Cm/Gm/Um.

(4) Figure 2H (left): Please comment on the few outliers that still show high non-conversion even in PCIF1-KO cells.

We thank the reviewer for this comment. We have discussed the outliers in the main text. These outliers can be found in the revised Table S3.

(5) Line 254: "Second, if these sites were RNA fragments they would not contain m6Am." is missing a comma.

(6) S2G and S2H labelling in Figure S2 legends is wrong.

For (5) and (6). We thank the reviewer for these comments. We have corrected them.

(7) Figure 3D: Many gene names are printed multiple times (e.g. ACTB is printed 5 times). Is this correct; is each dot representing 1 cell line?

We thank the reviewer for this comment. These gene names represent different transcription-start nucleotides. We now clarify that each instance refers to a different start site.

(8) S5A-C: Even if there's no substantial difference, authors should still display the Student's T-test P-values as they did for S5D-G.

We thank the reviewer for this comment. We have updated the P-values.

(9) Figure 5C and S5E: Why are the authors not showing the respective analysis for C-TSN and U-TSN genes?

We thank the reviewer for this comment. Most mRNAs start with A or G. We therefore selected G-TSN as the control. Unlike G-TSNs which occur in diverse sequence and promoter contexts, C-TSNs and U-TSNs are unusual. Genes that mainly use C-TSNs and U-TSNs are the so-called “5’ TOP (Terminal OligoPyrimidine)” genes. The 5’ TOP genes are mostly genes related to translation and metabolism, and thus their expressions reflect the homeostasis of cell metabolism. Thus, we were concerned that any differential expression of the C-TSN and U-TSN genes between wild-type and PCIF1 knockout cells might reflect specific effects on TOP transcriptional regulation rather than the general effects of PCIF1 on transcription.

(10) Line 82, 470, 506, 676: The authors should also cite Koh et al (2019 Nat. Comm.) in these lines that describe how snRNAs can also be m6Am-methylated and how FTO targets these same snRNAs for demethylation.

We thank the reviewer for this comment. We have updated the citation.

Author response:

We thank all the reviewers for their insightful comments on this work.

Response to Reviewer #1:

We greatly appreciate your comments on the general reliability and significance of our work. We fully agree that it would have been ideal to have additional evidence related to the role of PEBP1 in HRI activation. Unfortunately, we have not been able to find phospho-HRI antibodies that work reliably. The literature seems to agree with this as a band shift using total-HRI antibodies is usually used to study HRI activation. However, with the cell lines showing the most robust effect with PEBP1 knockout or knockdown, we are yet to convince ourselves with the band shifts we see. This could be addressed by optimizing phos-tag gels although these gels can be a bit tricky with complex samples such as cell lysates which contain many phosphoproteins.

To address the interaction between PEBP1 and eIF2alpha more rigorously we were inspired by the insights you and reviewer #2 provided. While we are unable to do further experiments, we now think it would indeed be possible to do this with either using the purified proteins and/or CETSA WB. These experiments could also provide further evidence for the role of PEBP1 phosphorylation. Although phosphorylation of PEBP1 at S153 has been implicated as being important for other functions of PEBP1, we are not sure about its role here. It may indeed have little relevance for ISR signalling.

For the in vitro thermal shift assay, we have performed two independent experiments. While it appears that there is a slight destabilization of PEBP1 by oligomycin, the ultimate conclusion of this experiment remains incomplete as there could be alternative explanations despite the apparent simplicity of the assay due the fluorescence background by oligomycin only. We now provide a lysate based CETSA analysis which does not display the same PEBP1 stabilization as the intact cell experiment. As for the signal saturation in ATF4-luciferase reporter assay, this is a valid point.

Response to Reviewer #2:

We strongly agree that CETSA has a lot of potential to inform us about cellular state changes and this was indeed the starting point for this project. We apologize for being (too) brief with the explanations of the TPP/MS-CETSA approach and we have now added a bit more detail. With regard to the cut-offs used for the mass spectrometry analysis, you are absolutely right that we did not establish a stringent cut-off that would show the specificity of each drug treatment. Our take on the data was that using the p values (and ignoring the fold-changes) of individual protein changes as in Fig 1D, we can see that mitochondrial perturbations display a coordinated response. We now realize that the downside of this representation is that it obscures the largest and specific drug effects. As mentioned in the response to Reviewer #1, we now also think that it would be possible to obtain more evidence for the potential interaction between PEBP1 and eIF2alpha using CETSA-based assays.

Response to Reviewer #3:

Thank you for your assessment, we agree that this manuscript would have been made much stronger by having clearer mechanistic insights. As mentioned in the responses to other reviewers above, we aim to address this limitation in part by looking at the putative interaction between PEBP1 and eIF2alpha with orthogonal approaches. However, we do realize that analysis of protein-protein interactions can be notoriously challenging due to false negative and false positive findings. As with any scientific endeavor, we will keep in mind alternative explanations to the observations, which could eventually provide that cohesive model explaining how precisely PEBP1, directly or indirectly, influences ISR signalling.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

The data overall are very solid, and I would only recommend the following minor changes: 

(1) Line 187 and line 268: there is perhaps a trend towards slightly increased ATF4-luc reporter with PEBP1-S153D, but it is not statistically significant, so I would tone down the wording here. 

We now modified this part to "This data is consistent with the modest increase…" .

(2) The recently discovered SIFI complex (Haakonsen 2024, https://doi.org/10.1038/s41586023-06985-7) regulates both HRI and DELE1 through bifunctional localization/degron motifs. It seems like PEBP1 also contains such a motif, which suggests a potential mechanism for enrichment near mitochondria, perhaps even in response to stress. Maybe the authors could further speculate on this in the discussion. 

While working on the manuscript, we considered the possibility that PEBP1 function could be related to SIFI complex and concluded that here is a critical difference: while  SIFI specifically acts to turn off stress response signalling, loss of PEBP1 prevents eIF2alpha phosphorylation. We did not however consider that PEBP1 could have a localization/degron motif. Motif analysis by deepmito (busca.biocomp.unibo.it) and similar tools did not identify any conventional mitochondrial targeting signal although we acknowledge that PEBP1 has a terminal alpha-helix which was identified for SIFI complex recognition. We are not sure why you think PEBP1 contains such a motif and therefore are hesitant to speculate on this further in the manuscript.

(3) Line 358: references 50 and 45 are identical. 

Thank you for spotting this. Corrected now. 

(4) Figure S1D: it looks like Oligomycin has a significant background fluorescence, which makes interpretation of these graphs difficult - do you have measurements of the compound alone that can be used to subtract this background from the data? Based on the Tm I would say it does stabilize recombinant PEBP1, and there is no quantification of the variance across the 3 replicates to say there is no difference. 

You are right, this assay is problematic due to the background fluorescence. The measurements with oligomycin only and subtracting this background results in slightly negative values and nonsensical thermal shift curves. We now additionally show quantification from two different experiments (unfortunately we ran out of reagents for further experiments), and this quantification shows that if anything, oligomycin causes mild destabilization of recombinant PEBP1. We also used lysate CETSA assay which does not show thermal stabilization of PEBP1 by oligomycin, ruling out a direct effect. We attempted to use ferrostatin1 as a positive control as it may bind PEBP1-ALOX protein complex, and it appeared to show marginal stabilization of PEBP1. 

Reviewer #2 (Recommendations for the authors): 

I have a few comments for the authors to address: 

(1) The MS-CETSA experiment is quite briefly described and this could be expanded somewhat. Not clear if multiple biological replicates are used. Is there any cutoff in data analysis based on fold change size (which correlated to the significance of cellular effects), etc? As expected from only one early timepoint (see eg PMID: 38328090), there appear to be a limited number of significant shifts over the background (as judged from Figure S1A). In the Excel result file, however (if I read it right) there are large numbers of proteins that are assigned as stabilized or destabilized. This might be to mark the direction of potential shifts, but considering that most of these are likely not hits, this labeling could give a false impression. Could be good to revisit this and have a column for what could be considered significant hits, where a fold change cutoff could help in selecting the most biologically relevant hits. This would allow Figure 1D to be made crisper when it likely dramatically overestimates the overlap between significant CETSA shifts for these drugs.  

Fair point, while we focused more on PEBP1, it is important to have sufficient description of the methods. We used duplicate samples for the MS, which is probably the most important point which was absent from the original submission as is now added to the methods. We also added slightly more description on the data analysis. While the AID method does not explicitly use log2 fold changes, it does consider the relative abundance of proteins under different temperature fractions. Since the Tm (melting temperature) for each protein can be at any temperature, we felt that if would be complicated to compare fractions where the protein stability is changed the most and even more so if we consider both significance and log2FC. Therefore, we used this multivariate approach which indicates the proteins with most likely changes across the range of temperatures. To acknowledge that most of the statistically significant changes are not the much over the background as you correctly pointed out, we now add to the main text that “However, most of these changes are relatively small. To focus our analysis on the most significant and biologically relevant changes…” We also agree that it may be confusing that the AID output reports de/stabilization direction for all proteins. In general, we are not big fans of cutoffs as these are always arbitrary, but with multivariate p value of 0.1 it becomes clear that there are only a relatively small number of hits with larger changes. We have now added to the guide in the data sheet that "Primarily, use the adjusted p value of the log10 Multivariate normal pvalue for selecting the overall statistically significant hits (p<0.05 equals  -1.30 or smaller; p<0.01 equals  -2 or smaller)". We have also added to the guide part of the table that “Note that this prediction does not consider whether the change is significant or not, it only shows the direction of change”

(2) On page 4 the authors state "We reasoned that thermal stability of proteins might be particularly interesting in the context of mitochondrial metabolism as temperature-sensitive fluorescent probes suggest that mitochondrial temperature in metabolically active cells is close to 50{degree sign}C". I don't see the relevance of this statement as an argument for using TPP/CETSA. When this is also not further addressed in the work, it could be deleted.

Deleted. We agree, while this is an interesting point, it is not that relevant in this paper. 

(3) To exclude direct drug binding to PEBP1, a thermofluor experiment is performed (Fig S1D). However, the experiment gives a high background at the lower temperatures and it could be argued that this is due to the flouroprobe binding to a hydrophobic pocket of the protein, and that oligomycin at higher concentrations competes with this binding, attenuating fluorescence. These are complex experiments and there could be other explanations, but the authors should address this. An alternative means to provide support for non-binding would be a lysate CETSA experiment, with very short (1-3 minutes) drug exposure before heating. This would typically give a shift when the protein is indicated to be CETSA responsive as in this case. 

Agree. However, we don't have good means to perform the thermofluor experiments to rule out alternative explanations. What we can say is (as discussed above for reviewer #1, point 4) that quantification from two different experiments shows that oligomycin is does not thermally stabilizing recombinant PEBP1. To complement this conclusion, we used lysate CETSA assay which does not show thermal stabilization of PEBP1 by oligomycin. In this assay we attempted to use ferrostatin1 as a positive control as it may bind PEBP1-ALOX protein complex, and it appeared to show marginal stabilization of PEBP1. But since we lack a robust positive control for these assays, some doubt will inevitably remain.

(4) The authors appear to have missed that there is already a MS-CETSA study in the literature on oligomycin, from Sun et al (PMID: 30925293). Although this data is from a different cell line and at a slightly longer drug treatment and is primarily used to access intracellular effects of decreased ATP levels induced by oligomycin, the authors should refer to this data and maybe address similarities if any.  

Apologies for the oversight, the oligomycin data from this paper eluded us at it was mainly presented in the supplementary data. We compared the two datasets and find found some overlap despite the differences in the experimental details. Both datasets share translational components (e.g. EIF6 and ribosomal proteins), but most notably our other top hit BANF1 which we mentioned in the main text was also identified by Sun et al. We have updated the manuscript text as "Other proteins affected by oligomycin included BANF1, which binds DNA in an ATP dependent manner [16], and has also identified as an oligomycin stabilized protein in a previous MS-CETA experiment [23]", citing the Sun et al paper.   

(5) The confirmation of protein-protein interaction is notoriously prone to false positives. The authors need to use overexpression and a sensitive reporter to get positive data but collect additional data using mutants which provide further support. Typically, this would be enough to confirm an interaction in the literature, although some doubt easily lingers. When the authors already have a stringent in-cell interaction assay for PEBP1 in the CETSA thermal shift, it would be very elegant to also apply the CETSA WB assay to the overexpressed constructs and demonstrate differences in the response of oligomycin, including the mutants. I am not sure this is feasible but it should be straightforward to test. 

This is a very good suggestion. Unfortunately, due to the time constraints of the graduate students (who must write up their thesis very soon), we are not able to perform and repeat such experiments to the level of confidence that we would like.

(6) At places the story could be hard to follow, partly due to the frequent introduction of new compounds, with not always well-stated rationale. It could be useful to have a table also in the main manuscript with all the compounds used, with the rationale for their use stated. Although some of the cellular pathways addressed are shown in miniatures in figures, it could be useful to have an introduction figure for the known ISR pathways, at least in the supplement. There are also a number of typos to correct. 

We agree that there are many compounds used. We have attempted to clarify their use by adding this information into the table of used compounds in the methods and adding an overall schematic to Fig S1G and a note on line 132 "(see Figure 1-figure supplement 1G for summary of drugs used to target PEBP1 and ISR in this manuscript). We have also attempted to remove typos as far as possible.

(7) EIF2a phosphorylation in S1E does not appear to be more significant for Sodium Arsenite argued to be a positive control, than CCCP, which is argued to be negative. Maybe enough with one positive control in this figure? 

This experiment was used as a justification for our 30 min time point for the proteomics. By showing the 30 min and 4 h time points as Fig 1G and Figure 1-figure supplement 1F, our point was to demonstrate that the kinetics of phosphorylation and dephosphorylation are relevant. As you correctly pointed out, the stress response induced by sodium arsenite, but also tunicamycin is already attenuated at the 4h time point. We prefer to keep all samples to facilitate comparisons.

(8) Page 7 reference to Figure S2H, which doesn't exist. Should be S3H.  

Apologies for the mistake, now corrected to Figure 2-figure supplement 1B.

(9) Finally, although the TPP labeling of the method is used widely in the literature this is CETSA with MS detection and MS-CETSA is a better term. This is about thermal shifts of individual proteins which is a very well-established biophysical concept. In contrast, the term Thermal Proteome Profiling does not relate to any biophysical concept, or real cell biology concept, as far as I can see, and is a partly misguided term. 

We changed the term TPP into MS-CETSA, but also include the term TPP in the introduction to facilitate finding this paper by people using the TPP term.

Reviewer #3 (Recommendations for the authors): 

Major Issues 

(1) The one major issue of this work is the lack of a mechanism showing precisely how PEBP1 amplifies the mitochondrial integrated stress response. The work, as it is described, presents data suggesting PEBP1's role in the ISR but fails to present a more conclusive mechanism. The idea of mitochondrial stress causing PEBP1 to bind to eIF2a, amplifying ISR is somewhat vague. Thus, the lack of a more defined model considerably weakens the argument, as the data is largely corollary, showing KO and modulation of PEBP1 definitely has a unique effect on the ISR, however, it is not conclusive proof of what the authors claim. While KO of PEBP1 diminishes the phosphorylation of eIF2a, taken together with the binding to eIF2a, different pathways could be simultaneously activated, and it seems premature to surmise that PEBP1 is specific to mitochondrial stress. Could PEBP1 be reacting to decreased ATP? Release of a protein from the mitochondria in response to stress? Is PEBP1's primary role as a modulator of the ISR, or does it have a role in non-stress-related translation? A cohesive model would tie together these separate indirect findings and constitute a considerable discovery for the ISR field, and the mitochondrial stress field.  

Thank you for your assessment, we agree that this manuscript would have been much stronger by having clearer mechanistic insights. As with any scientific endeavor, we will keep in mind alternative explanations to the observations, which could eventually provide that cohesive model explaining how precisely PEBP1, directly or indirectly, influences ISR signalling.

(2) The data relies on the initial identification of PEBP1 thermal stabilization concomitant with mitochondrial ISR induction post-treatment of several small molecules. However, the experiment was performed using a single timepoint of 30 minutes. There was no specific rationale for the choice of this time point for the thermal proteome profiling. 

The reasoning for this was explicitly stated:  "We reasoned that treating intact cells with the drugs for only 30 min would allow us to observe rapid and direct effects related to metabolic flux and/or signaling related to mitochondrial dysfunction in the absence of major changes in protein expression levels.”

Minor Issues 

(1) In Lines 163-166 the authors state "The cells from Pebp1 KO animals displayed reduced expression of common ISR genes (Figure 2F), despite upregulation of unfolded protein response genes Ern1 (Ire1α) and Atf6 genes. This gene expression data therefore suggests that Pebp1 knockout in vivo suppresses induction of the ISR". This statement should be reassessed. While an arm of the UPR does stimulate ISR, this arm is controlled by PERK, and canonically IRE1 and ATF6 do not typically activate the ISR, thus their upregulation is likely unrelated to ISR activation and does not contribute the evidence necessary for this statement. 

Apologies for the confusion, we aimed to highlight that as there is an increase in the two UPR arms, it is more likely that ISR instead of UPR is reduced. We have now changed the statement to the following:

"The cells from Pebp1 PEBP1 KO animals displayed reduced expression of common ISR genes (Figure 2F), while there was mild upregulation of the unfolded protein response genes Ern1 (Ire1α) and Atf6 genes. This gene expression data therefore suggests that the reduced expression of common ISR genes is less likely to be mediated by changes in PERK, the third UPR arm, and more likely due to suppression of ISR by Pebp1 knockout in vivo."

(2) In Lines 169 and 170 the authors state "Western blotting indicated reduced phosphorylation of eIF2α in RPE1 cells lacking PEBP1, suggesting that PEBP1 is involved in regulating ISR signaling between mitochondria and eIF2α". This conclusion is not supported by evidence. A number of pathways could be activated in these knockout cells, and simply observing an increase in p-eIF2α after knocking out PEBP1 does not constitute an interaction, as correlation doesn't mean causation. This KO could indirectly affect the ISR, with PEBP1 having no role in the ISR. While taken together there is enough circumstantial evidence in the manuscript to suggest a role for PEBP1 in the ISR, statements such as these have to be revised so as not to overreach the conclusions that can be achieved from the data, especially with no discernible mechanism.  

We have now revised this statement by removing the conclusion and stating only the observation:  "Western blotting indicated reduced phosphorylation of eIF2α in RPE1 cells lacking PEBP1 (Fig. 3A)."

Author response:

Reviewer #2 (Public Review): 

Comment 1: In terms of the biological significance of this interaction, it would be good to examine (via co-immunoprecipitation) whether the CEP89/NCS-1/C3ORF14 interaction takes place upon serum starvation. Does the complex change? 

NCS1 centriolar localization requires CEP89 as no NCS1 localization was observed in CEP89 knockout cells (Figure 2L; Figure 2-figure supplement 2B). Both CEP89 and NCS1 centriolar localization were observed (Figure 2C; Figure 1D of the PMID: 36711481) in cells grown in serum containing media, although their localization was further enhanced in serum starved cells. From these results, we predict that CEP89 and NCS1 can interact and colocalize in both serum-fed and serum-depleted condition. We think it may not be easy to assess the change in interaction with the co-immunoprecipitation assay, as interactions occur in a test tube, which may not reflect the binding condition inside the cells.

Comment 2: Also, for the subdistal appendage localization of NCS-1 and C3ORF14, would this also change upon serum starvation? 

We agree that it would be interesting to see whether the subdistal appendage localization changes upon serum starvation, as NCS1 may capture the ciliary vesicle at the subdistal appendages as we discussed. However, the loss of the subdistal appendage protein, CEP128, blocks subdistal appendage localization of CEP89 [PMID: 32242819] without affecting cilium formation [PMID: 27818179]. This suggests that the subdistal appendage localization of NCS1 or C3ORF14 is likely dispensable for cilium formation.

Comment 3: For the ciliation results and the recruitment of IFT88 in CEP89 knockout cell lines, this contradicts previous work from Tanos et al (PMID: 23348840), as well as Hou et al (PMID: 36669498). A parallel comparison using siRNA, a transient knockout system, or a degron system would help understand this. A similar point goes for Figure 4, where the effect on ciliogenesis is minimal in knockout cells, but acute siRNA has been shown to have a stronger phenotype. 

Hou et al. [PMID: 36669498] investigated the role of distal appendage proteins, CEP164, CEP89, and FBF1 in the ciliated chordotonal organ of Drosophila melanogaster by generating knockout Drosophila strains. The results were markedly different from what was observed in mammalian cells. Notably, CEP164 is not required for cilium formation, and CEP89 is required for FBF1 localization in the animal. CEP89 was required for cilium formation in the cells in the ciliated chordotonal organ, of which cilium formation is dependent on IFT machinery. They did not show if IFT centriolar recruitment is affected in the CEP89 mutant cells. These differences likely reflect the divergence of the organization of distal appendage during evolution.

The ciliation phenotype of our CEP89 knockout cells are milder than what was shown in Tanos et al [PMID: 23348840], but largely consistent with the results from Bornens group, which used siRNA to deplete CEP89 [PMID: 23789104]. Besides, NCS1 knockout cells showed very similar phenotype to the CEP89 knockout cells, and relatively acute deletion of NCS1 (14 days after infection of the lenti-virus containing sgNCS1 without single-cell cloning) displayed an almost identical ciliation defect (Figure 4B-C). Thus, we believe CEP89 is only partially required for cilium formation in RPE-hTERT cells and that the differences are more technical than definitive.

Comment 4: An elegant phenotype rescue is shown in Figure 5. An interesting question would be, how does this mutant and/or the myristoylation affect the recruitment of C3ORF14? 

NCS1 is not required for the localization of C3ORF14 (Figure 2M; Figure 2- figure supplement 2C), so we can assume that the myristoylation defective mutant does not affect C3ORF14 recruitment.

Comment 5: For the EF-hand mutants, it would be good to use control mutants, from known Ca2+ binding proteins as a control for the experiment shown. 

In the Figure 5-figure supplement 1A-C, we generated a series of EF-hand mutant of NCS1 to see if the calcium binding affects the CEP89 interaction, NCS1 localization, and cilium formation. NCS1 is only protein among the calcium binding NCS family proteins that was found as a positive hit in the mass spec data of CEP89 tandem affinity purification. Therefore, we cannot use other NCS1 family proteins as a control for CEP89 binding, NCS1 localization, and cilium formation.