Author Response

Reviewer #1 (Public Review):

Esmaily and colleagues report two experimental studies in which participants make simple perceptual decisions, either in isolation or in the context of a joint decision-making procedure. In this "social" condition, participants are paired with a partner (in fact, a computer), they learn the decision and confidence of the partner after making their own decision, and the joint decision is made on the basis of the most confident decision between the participant and the partner. The authors found that participants' confidence, response times, pupil dilation, and CPP (i.e. the increase of centro-parietal EEG over time during the decision process) are all affected by the overall confidence of the partner, which was manipulated across blocks in the experiments. They describe a computational model in which decisions result from a competition between two accumulators, and in which the confidence of the partner would be an input to the activity of both accumulators. This model qualitatively produced the variation in confidence and RTs across blocks.

The major strength of this work is that it puts together many ingredients (behavioral data, pupil and EEG signals, computational analysis) to build a picture of how the confidence of a partner, in the context of joint decision-making, would influence our own decision process and confidence evaluations. Many of these effects are well described already in the literature, but putting them all together remains a challenge.

We are grateful for this positive assessment.

However, the construction is fragile in many places: the causal links between the different variables are not firmly established, and it is not clear how pupil and EEG signals mediate the effect of the partner's confidence on the participant's behavior.

We have modified the language of the manuscript to avoid the implication of a causal link.

Finally, one limitation of this setting is that the situation being studied is very specific, with a joint decision that is not the result of an agreement between partners, but the automatic selection of the most confident decisions. Thus, whether the phenomena of confidence matching also occurs outside of this very specific setting is unclear.

We have now acknowledged this caveat in the discussion in line 485 to 504. The final paragraph of the discussion now reads as follows:

“Finally, one limitation of our experimental setup is that the situation being studied is confined to the design choices made by the experimenters. These choices were made in order to operationalize the problem of social interaction within the psychophysics laboratory. For example, the joint decisions were not made through verbal agreement (Bahrami et al., 2010, 2012). Instead, following a number of previous works (Bang et al., 2017, 2020) joint decisions were automatically assigned to the most confident choice. In addition, the partner’s confidence and choice were random variables drawn from a distribution prespecified by the experimenter and therefore, by design, unresponsive to the participant’s behaviour. In this sense, one may argue that the interaction partner’s behaviour was not “natural” since they did not react to the participant's confidence communications (note however that the partner’s confidence and accuracy were not entirely random but matched carefully to the participant’s behavior prerecorded in the individual session). How much of the findings are specific to these experimental setting and whether the behavior observed here would transfer to real-life settings is an open question. For example, it is plausible that participants may show some behavioral reaction to a human partner’s response time variations since there is some evidence indicating that for binary choices such as those studied here, response times also systematically communicate uncertainty to others (Patel et al., 2012). Future studies could examine the degree to which the results might be paradigm-specific.”

Reviewer #2 (Public Review):

This study is impressive in several ways and will be of interest to behavioral and brain scientists working on diverse topics.

First, from a theoretical point of view, it very convincingly integrates several lines of research (confidence, interpersonal alignment, psychophysical, and neural evidence accumulation) into a mechanistic computational framework that explains the existing data and makes novel predictions that can inspire further research. It is impressive to read that the corresponding model can account for rather non-intuitive findings, such as that information about high confidence by your collaborators means people are faster but not more accurate in their judgements.

Second, from a methodical point of view, it combines several sophisticated approaches (psychophysical measurements, psychophysical and neural modelling, electrophysiological and pupil measurements) in a manner that draws on their complementary strengths and that is most compelling (but see further below for some open questions). The appeal of the study in that respect is that it combines these methods in creative ways that allow it to answer its specific questions in a much more convincing manner than if it had used just either of these approaches alone.

Third, from a computational point of view, it proposes several interesting ways by which biologically realistic models of perceptual decision-making can incorporate socially communicated information about other's confidence, to explain and predict the effects of such interpersonal alignment on behavior, confidence, and neural measurements of the processes related to both. It is nice to see that explicit model comparison favor one of these ways (top-down driving inputs to the competing accumulators) over others that may a priori have seemed more plausible but mechanistically less interesting and impactful (e.g., effects on response boundaries, no-decision times, or evidence accumulation).

Fourth, the manuscript is very well written and provides just the right amount of theoretical introduction and balanced discussion for the reader to understand the approach, the conclusions, and the strengths and limitations.

Finally, the manuscript takes open science practices seriously and employed preregistration, a replication sample, and data sharing in line with good scientific practice.

We are grateful to the reviewer for their positive assessment of our work.

Having said all these positive things, there are some points where the manuscript is unclear or leaves some open questions. While the conclusions of the manuscript are not overstated, there are unclarities in the conceptual interpretation, the descriptions of the methods, some procedures of the methods themselves, and the interpretation of the results that make the reader wonder just how reliable and trustworthy some of the many findings are that together provide this integrated perspective.

We hope that our modifications and revisions in response to the criticisms listed below will be satisfactory. To avoid redundancies, we have combined each numbered comment with the corresponding recommendation for the Authors.

First, the study employs rather small sample sizes of N=12 and N=15 and some of the effects are rather weak (e.g., the non-significant CPP effects in study 1). This is somewhat ameliorated by the fact that a replication sample was used, but the robustness of the findings and their replicability in larger samples can be questioned.

Our study brings together questions from two distinct fields of neuroscience: perceptual decision making and social neuroscience. Each of these two fields have their own traditions and practical common sense. Typically, studies in perceptual decision making employ a small number of extensively trained participants (approximately 6 to 10 individuals). Social neuroscience studies, on the other hand, recruit larger samples (often more than 20 participants) without extensive training protocols. We therefore needed to strike a balance in this trade-off between number of participants and number of data points (e.g. trials) obtained from each participant. Note, for example, that each of our participants underwent around 4000 training trials. Strikingly, our initial study (N=12) yielded robust results that showed the hypothesized effects nearly completely, supporting the adequacy of our power estimate. However, we decided to replicate the findings because, like the reviewer, we believe in the importance of adequate sampling. We increased our sample size to N=15 participants to enhance the reliability of our findings. However, we acknowledge the limitation of generalizing to larger samples, which we have now discussed in our revised manuscript and included a cautionary note regarding further generalizations.

To complement our results and add a measure of their reliability, here we provide the results of a power analysis that we applied on the data from study 1 (i.e. the discovery phase). These results demonstrate that the sample size of study 2 (i.e. replication) was adequate when conditioned on the results from study 1 (see table and graph pasted below). The results showed that N=13 would be an adequate sample size for 80% power for behavoural and eye-tracking measurements. Power analysis for the EEG measurements indicated that we needed N=17. Combining these power analyses. Our sample size of N=15 for Study 2 was therefore reasonably justified.

We have now added a section to the discussion (Lines 790-805) that communicates these issues as follows:

“Our study brings together questions from two distinct fields of neuroscience: perceptual decision making and social neuroscience. Each of these two fields have their own traditions and practical common sense. Typically, studies in perceptual decision making employ a small number of extensively trained participants (approximately 6 to 10 individuals). Social neuroscience studies, on the other hand, recruit larger samples (often more than 20 participants) without extensive training protocols. We therefore needed to strike a balance in this trade-off between number of participants and number of data points (e.g. trials) obtained from each participant. Note, for example, that each of our participants underwent around 4000 training trials. Importantly, our initial study (N=12) yielded robust results that showed the hypothesized effects nearly completely, supporting the adequacy of our power estimate. However, we decided to replicate the findings in a new sample with N=15 participants to enhance the reliability of our findings and examine our hypothesis in a stringent discovery-replication design. In Figure 4-figure supplement 5, we provide the results of a power analysis that we applied on the data from study 1 (i.e. the discovery phase). These results demonstrate that the sample size of study 2 (i.e. replication) was adequate when conditioned on the results from study 1.”

We conducted Monte Carlo simulations to determine the sample size required to achieve sufficient statistical power (80%) (Szucs & Ioannidis, 2017). In these simulations, we utilized the data from study 1. Within each sample size (N, x-axis), we randomly selected N participants from our 12 partpincats in study 1. We employed the with-replacement sampling method. Subsequently, we applied the same GLMM model used in the main text to assess the dependency of EEG signal slopes on social conditions (HCA vs LCA). To obtain an accurate estimate, we repeated the random sampling process 1000 times for each given sample size (N). Consequently, for a given sample size, we performed 1000 statistical tests using these randomly generated datasets. The proportion of statistically significant tests among these 1000 tests represents the statistical power (y-axis). We gradually increased the sample size until achieving an 80% power threshold, as illustrated in the figure.The the number indicated by the red circle on the x axis of this graph represents the designated sample size.

Second, the manuscript interprets the effects of low-confidence partners as an impact of the partner's communicated "beliefs about uncertainty". However, it appears that the experimental setup also leads to greater outcome uncertainty (because the trial outcome is determined by the joint performance of both partners, which is normally reduced for low-confidence partners) and response uncertainty (because subjects need to consider not only their own confidence but also how that will impact on the low-confidence partner). While none of these other possible effects is conceptually unrelated to communicated confidence and the basic conclusions of the manuscript are therefore valid, the reader would like to understand to what degree the reported effects relate to slightly different types of uncertainty that can be elicited by communicated low confidence in this setup.

We appreciate the reviewer’s advice to remain cautious about the possible sources of uncertainty in our experiment. In the Discussion (lines 790-801) we have now added the following paragraph.

“We have interpreted our findings to indicate that social information, i.e. partner’s confidence, impacts the participants beliefs about uncertainty. It is important to underscore here that, similar to real life, there are other sources of uncertainty in our experimental setup that could affect the participants' belief. For example, under joint conditions, the group choice is determined through the comparison of the choices and confidences of the partners. As a result, the participant has a more complex task of matching their response not only with their perceptual experience but also coordinating it with the partner to achieve the best possible outcome. For the same reason, there is greater outcome uncertainty under joint vs individual conditions. Of course, these other sources of uncertainty are conceptually related to communicated confidence but our experimental design aimed to remove them, as much as possible, by comparing the impact of social information under high vs low confidence of the partner.”

In addition to the above, we would like to clarify one point here with specific respect to the comment. Note that the computer-generated partner’s accuracy was identical under high and low confidence. In addition, our behavioral findings did not show any difference in accuracy under HCA and LCA conditions. As a consequence, the argument that “the trial outcome is determined by the joint performance of both partners, which is normally reduced for low-confidence partners)” is not valid because the low-confidence partner’s performance is identical to that of the high-confidence partner. It is possible, of course, that we have misunderstood the reviewer’s point here and we would be happy to discuss this further if necessary.

Third, the methods used for measurement, signal processing, and statistical inference in the pupil analysis are questionable. For a start, the methods do not give enough details as to how the stimuli were calibrated in terms of luminance etc so that the pupil signals are interpretable.

Here we provide in Author response image 1 the calibration plot for our eye tracking setup, describing the relationship between pupil size and display luminance. Luminance of the random dot motion stimuli (ie white dots on black background) was Cd/m2 and, importantly, identical across the two critical social conditions. We hope that this additional detail satisfies the reviewer’s concern. For the purpose of brevity, we have decided against adding this part to the manuscript and supplementary material.

Author response image 1.

Calibration plot for the experimental setup. Average pupil size (arbitrary units from eyelink device) is plotted against display luminance. The plot is obtained by presenting the participant with uniform full screen displays with 10 different luminance levels covering the entire range of the monitor RGB values (0 to 255) whose luminance was separately measured with a photometer. Each display lasted 10 seconds. Error bars are standard deviation between sessions.

Moreover, while the authors state that the traces were normalized to a value of 0 at the start of the ITI period, the data displayed in Figure 2 do not show this normalization but different non-zero values. Are these data not normalized, or was a different procedure used? Finally, the authors analyze the pupil signal averaged across a wide temporal ITI interval that may contain stimulus-locked responses (there is not enough information in the manuscript to clearly determine which temporal interval was chosen and averaged across, and how it was made sure that this signal was not contaminated by stimulus effects).

We have now added the following details to the Methods section in line 1106-1135.

“In both studies, the Eye movements were recorded by an EyeLink 1000 (SR- Research) device with a sampling rate of 1000Hz which was controlled by a dedicated host PC. The device was set in a desktop and pupil-corneal reflection mode while data from the left eye was recorded. At the beginning of each block, the system was recalibrated and then validated by 9-point schema presented on the screen. For one subject was, a 3-point schema was used due to repetitive calibration difficulty. Having reached a detection error of less than 0.5°, the participants proceeded to the main task. Acquired eye data for pupil size were used for further analysis. Data of one subject in the first study was removed from further analysis due to storage failure.

Pupil data were divided into separate epochs and data from Inter-Trials Interval (ITI) were selected for analysis. ITI interval was defined as the time between offset of trial (t) feedback screen and stimulus presentation of trial (t+1). Then, blinks and jitters were detected and removed using linear interpolation. Values of pupil size before and after the blink were used for this interpolation. Data was also mid-pass filtered using a Butterworth filter (second order,[0.01, 6] Hz)[50]. The pupil data was z-scored and then was baseline corrected by removing the average of signal in the period of [-1000 0] ms interval (before ITI onset). For the statistical analysis (GLMM) in Figure 2, we used the average of the pupil signal in the ITI period. Therefore, no pupil value is contaminated by the upcoming stimuli. Importantly, trials with ITI>3s were excluded from analysis (365 out of 8800 for study 1 and 128 out 6000 for study 2. Also see table S7 and Selection criteria for data analysis in Supplementary Materials)”

Fourth, while the EEG analysis in general provides interesting data, the link to the well-established CPP signal is not entirely convincing. CPP signals are usually identified and analyzed in a response-locked fashion, to distinguish them from other types of stimulus-locked potentials. One crucial feature here is that the CPPs in the different conditions reach a similar level just prior to the response. This is either not the case here, or the data are not shown in a format that allows the reader to identify these crucial features of the CPP. It is therefore questionable whether the reported signals indeed fully correspond to this decision-linked signal.

Fifth, the authors present some effective connectivity analysis to identify the neural mechanisms underlying the possible top-down drive due to communicated confidence. It is completely unclear how they select the "prefrontal cortex" signals here that are used for the transfer entropy estimations, and it is in fact even unclear whether the signals they employ originate in this brain structure. In the absence of clear methodical details about how these signals were identified and why the authors think they originate in the prefrontal cortex, these conclusions cannot be maintained based on the data that are presented.

Sixth, the description of the model fitting procedures and the parameter settings are missing, leaving it unclear for the reader how the models were "calibrated" to the data. Moreover, for many parameters of the biophysical model, the authors seem to employ fixed parameter values that may have been picked based on any criteria. This leaves the impression that the authors may even have manually changed parameter values until they found a set of values that produced the desired effects. The model would be even more convincing if the authors could for every parameter give the procedures that were used for fitting it to the data, or the exact criteria that were used to fix the parameter to a specific value.

Seventh, on a related note, the reader wonders about some of the decisions the authors took in the specification of their model. For example, why was it assumed that the parameters of interest in the three competing models could only be modulated by the partner's confidence in a linear fashion? A non-linear modulation appears highly plausible, so extreme values of confidence may have much more pronounced effects. Moreover, why were the confidence computations assumed to be finished at the end of the stimulus presentation, given that for trials with RTs longer than the stimulus presentation, the sensory information almost certainly reverberated in the brain network and continued to be accumulated (in line with the known timing lags in cortical areas relative to objective stimulus onset)? It would help if these model specification choices were better justified and possibly even backed up with robustness checks.

Eight, the fake interaction partners showed several properties that were highly unnatural (they did not react to the participant's confidence communications, and their response times were random and thus unrelated to confidence and accuracy). This questions how much the findings from this specific experimental setting would transfer to other real-life settings, and whether participants showed any behavioral reactions to the random response time variations as well (since several studies have shown that for binary choices like here, response times also systematically communicate uncertainty to others). Moreover, it is also unclear how the confidence convergence simulated in Figure 3d can conceptually apply to the data, given that the fake subjects did not react to the subject's communicated confidence as in the simulation.

Author Response

Reviewer #1 (Public Review):

This work by Shen et al. demonstrates a single molecule imaging method that can track the motions of individual protein molecules in dilute and condensed phases of protein solutions in vitro. The authors applied the method to determine the precise locations of individual molecules in 2D condensates, which show heterogeneity inside condensates. Using the time-series data, they could obtain the displacement distributions in both phases, and by assuming a two-state model of trapped and mobile states for the condensed phase, they could extract diffusion behaviors of both states. This approach was then applied to 3D condensate systems, and it was shown that the estimates from the model (i.e., mobile fraction and diffusion coefficients) are useful to quantitatively compare the motions inside condensates. The data can also be used to reconstruct the FRAP curves, which experimentally quantify the mobility of the protein solution.

This work introduces an experimental method to track single molecules in a protein solution and analyzes the data based on a simple model. The simplicity of the model helps a clear understanding of the situation in a test tube, and I think that the model is quite useful in analyzing the condensate behaviors and it will benefit the field greatly. However, the manuscript in its current form fails to situate the work in the right context; many previous works are omitted in this manuscript, exaggerating the novelty of the work. Also, the two- state model is simple and useful, but I am concerned about the limits of the model. They extract the parameters from the experimental data by assuming the model. It is also likely that the molecules have a continuum between fully trapped and fully mobile states, and that this continuum model can also explain the experimental data well.

We thank the reviewer for the warm overview of our work and the insightful comments on the areas that need to be improved. We are very encouraged by the reviewer’s general positive assessment of our approach. We have addressed these comments in the revised manuscript

Reviewer #2 (Public Review):

In this paper, Shen and co-workers report the results of experiments using single particle tracking and FRAP combined with modeling and simulation to study the diffusion of molecules in the dense and dilute phases of various kinds of condensates, including those with strong specific interactions as well as weak specific interactions (IDR-driven). Their central finding is that molecules in the dense phase of condensates with strong specific interactions tend to switch between a confined state with low diffusivity and a mobile state with a diffusivity that is comparable to that of molecules in the dilute phase. In doing so, the study provides experimental evidence for the effect of molecular percolation in biomolecular condensates.

Overall, the experiments are remarkably sophisticated and carefully performed, and the work will certainly be a valuable contribution to the literature. The authors' inquiry into single particle diffusivity is useful for understanding the dynamics and exchange of molecules and how they change when the specific interaction is weak or strong. However, there are several concerns regarding the analysis and interpretation of the results that need to be addressed, and some control experiments that are needed for appropriate interpretation of the results, as detailed further below.

We thank the reviewer for the warm support of our work (assessing that our work is “remarkably sophisticated and carefully performed” and “will certainly be a valuable contribution”) and for the constructive comments/critiques, which we have now addressed in the revised manuscript (please refer to our detailed responses below).

(1) The central finding that the molecules tend to experience transiently confined states in the condensed phase is remarkable and important. This finding is reminiscent of transient "caging"/"trapping" dynamics observed in diverse other crowded and confined systems. Given this, it is very surprising to see the authors interpret the single-molecule motion as being 'normal' diffusion (within the context of a two-state diffusion model), instead of analyzing their data within the context of continuous time random walks or anomalous diffusion, which is generally known to arise from transient trapping in crowded/confined systems. It is not clear that interpreting the results within the context of simple diffusion is appropriate, given their general finding of the two confined and mobile states. Such a process of transient trapping/confinement is known to lead to transient subdiffusion at short times and then diffusive behavior at sufficiently long times. There is a hint of this in the inset of Fig 3, but these data need to be shown on log-log axes to be clearly interpreted. I encourage the authors to think more carefully and critically about the nature of the diffusive model to be used to interpret their results.

We thank the reviewer for the insightful comments and suggestions, which have been very helpful for us to think deeper about the experimental data and the possible underlying mechanism of our findings. Indeed, the phase separated systems studied here resemble previously studied crowed and confined systems with transient caging/trapping dynamics in the literature ((Akimoto et al., 2011; Bhattacharjee and Datta, 2019; Wong et al., 2004) for examples)(references have been added in the revised manuscript). In our PSD system in Figure 3, The caging/trapping of NR2B in the condensed phase is likely due to its binding to the percolated PSD network. Thus, NR2B molecules in the condensed phase should undergo subdiffusive motions. Indeed, from our single molecule tracking data, the motion of NR2B fits well with the continuous time random walk (CTRW) model, as surmised by this reviewer. We have now fitted the MSD curve of all tracks of NR2B in the condensed phase with an anomalous diffusion model: MSD(t)=4Dtα (see Response Figure 1 below). The fitted α is 0.74±0.03, indicating that NR2B molecules in the condensed phase indeed undergo sub- diffusive motions. The fitted diffusion coefficient D is 0.014±0.001 μm2/s. We have now replaced the Brownian motion fitting in Figure 3E in the original manuscript with this sub- diffusive model fitting in the revised manuscript to highlight the complexity of NR2B diffusion in PSD condensed phase we observed.

Response Figure 1: Fitted the MSD curve (mean value as red dot with standard error as error bar) in condensed phase with an anomalous diffusion model (blue curve, MSD=4Dtα). The fitting gives D=0.014±0.001 μm2/s and α=0.74±0.03.

We find it useful to interpret the apparent diffusion coefficient (D=0.014±0.001 μm2/s) derived from this particular anomalous diffusion model as containing information of NR2B motions in a broadly construed mobile state (i.e., corresponding to the network unbound form) as well as in a broadly construed confined state (i.e., corresponding to NR2B molecules bound to percolated PSD networks). The global fitting using the sub-diffusive model does not pin down motion properties of NR2B in these different motion states. This is why we used, at least as a first approximation, the two-state motion switch model (HMM model) to analyse our data (please refer also to our detailed response to the comment #7 from reviewer 1 and corresponding additional analyses made during the revision as highlighted in Response Figure 4).

As described in our response to the comment points #4 and #7 from reviewer 1, the two- state model is most likely a simplification of NR2B motions in the condensed phase. Both the mobile state and the confined state in our simplified interpretative framework likely represent ensemble averages of their respective motion states. However, the tracking data available currently do not allow us to further distinguish the substates, but further analysis using more refined model in the future may provide more physical insight, as we now emphasize in the revised “Discussion” section: “With this in mind, the two motion states in our simple two-state model for condensed-phase dynamics should be understood to be consisting of multiple sub-states. For instance, one might envision that the percolated molecular network in the condensed phase is not uniform (e.g., existence of locally denser or looser local networks) and dynamic (i.e., local network breaking and forming). Therefore, individual proteins binding to different sub-regions of the network will have different motion properties/states. … In light of this basic understanding, the “confined state” and “mobile state” as well as the derived diffusion coefficients in this work should be understood as reflections of ensemble-averaged properties arising from such an underlying continuum of mobilities. Further development of experimental techniques in conjunction with more refined models of anomalous diffusion (Joo et al., 2020; Kuhn et al., 2021; Muñoz-Gil et al., 2021) will be necessary to characterize these more subtle dynamic properties and to ascertain their physical origins” (p.23 of the revised manuscript).

A practical reason for using the two-state motion switch HMM model to analyse our tracking data in the condensed phase is that the lifetime of the putative mobile state (when the per-frame molecular displacements are relatively large) is very short and such relatively faster short trajectories are interspersed by long confined states (see Response Figure 4C for an example). Statistically, ascertaining a particular anomalous diffusion model by fitting to such short tracks is likely not reliable. Therefore, here we opted for a semi-quantitative interpretative framework by using fitted diffusion coefficients in a two-state HMM as well as the new correlation-based approach for demarcating a low-mobility state and a high- mobility state (see our detailed response to reviewer 1’s point #7) in the present manuscript (which is quite an extensive study already) while leaving refinements of our computational modelling to future effort.

Even in the context of the 'normal' two-state diffusion model they present, if they wish to stick with that-although it seems inappropriate to do so-can the authors provide some physical intuition for what exactly sets the diffusivities they extract from their data. (0.17 and 0.013 microns squared per second for the mobile and confined states). Can these be understood using e.g., the Stoke-Einstein or Ogston models somehow?

As stated above, we are in general agreement with this reviewer that the motion of NR2B in the condensed phase is more complex than the simple two-state picture we adopted as a semi-quantitative interpretation that is adequate for our present purposes. Within the multi-pronged analysis we have performed thus far, NR2B molecules clearly undergo anomalous diffusions in solution containing dense, percolated, and NR2B-binding molecular networks. As a first approximation, our simple two-state HMM analysis yielded two simple diffusion coefficients (0.17 μm2/s for the mobile state and 0.013 μm2/s for the confined state). For the diffusion coefficient in the mobile state, we regard it as providing a time scale for relatively faster diffusive motions (which may be further classified into various motion substates in the future) that are not bound or only weakly associated with the percolated network of strong interactions in the PSD condensed phase. For the confined or low-mobility state in our present formulation, these molecules are likely bound relatively tightly to the percolated networks, thus the diffusion coefficient should be much smaller than the unbounded form (i.e., the mobile state) according to the Stoke-Einstein model. However, due to the detection limitation of the supper resolution imaging method (resolution of ~20 nm), we could not definitively tell the actual diffusivity beyond the resolution limit. So the diffusion coefficient in the confined state can also be interpreted as a Gaussian distributed microscope detection error (𝑓(𝑥) =1 , which is x~N(0, σ2), where σ is the standard deviation of the Gaussian distribution viewed as the resolution of localization-based microscopy, x is the detection error between recorded localization and molecule’s actual position). The track length in the confined state is the distance between localizations in consecutive frames, which can be calculated by subtraction of two independent Gaussian distributions, and the distribution of this track length (r) will be r~N(0, 2σ2). To link the detection error with the fitted diffusion coefficient, we calculated the log likelihood function of Gaussian distributed localization error (, where σ is the standard deviation of the Gaussian distribution) for the maximum likelihood estimation process to fit the HMM model. The random walk shares a similar log likelihood term () in performing maximum likelihood estimation.

These two log likelihood functions will produce same fitting results with 2σ2 equivalent to 4Dt according to the likelihood function. In this way, the diffusion coefficient yielded by our HMM analyses for the confined state (0.0127 μm2/s) can be interpreted as the standard deviation of localization detection error (or microscope resolution limit), which is 𝜎 =√2𝐷𝑡 = 19.5 𝑛𝑚. We have included this consideration as an alternate interpretation of the confined-state or low-mobility motions with the results now provided in the “Materials and Methods” section in the sentence, viz., “… the L-component distribution may be reasonably fitted (albeit with some deviations, see below) to a simple-diffusion functional form with a parameter s =13.6 ± 3.7 nm, where s may be interpreted as a microscope detection error due to imaging limits or alternately expressed as s = DLt with DL = 0.006149 μm2/s being the fitted confined-state diffusion coefficient and t = 0.03s is the time interval of the time step between experimental frames. (The HMM-estimated confined-state Dc = 0.0127 μm2/s corresponds to s = 19.5 nm)” (p.32 of the revised manuscript).

(2) Equation 1 (and hence equation 2) is concerning. Consider a limit when P_m=1, that is, in the condensed phase, there are no confined particles, then the model becomes a diffusion equation with spatially dependent diffusivity, \partial c /\partial t = \nabla * (D(x) \nabla c). The molecules' diffusivity D(x) is D_d in the dilute phase and D_m in the condensed phase. No matter what values D_d and D_m are, at equilibrium the concentration should always be uniform everywhere. According to Equation 1, the concentration ratio will be D_d/D_m, so if D_d/D_m \neq 1, a concentration gradient is generated spontaneously, which violates the second law of thermodynamics. Can the authors please justify the use of this equation?

Indeed, the derivation of Equation 1 appears to be concerning. The flux J is proportional to D * dc/dx (not kDc as in the manuscript). At equilibrium dc/dx = 0 on both sides and c is constant everywhere. Can the authors please comment?

So then another question is, why does the Monte Carlo simulation result agree with Equation 1? I suspect this has to do with the behavior of particles crossing the boundary. Consider another limit where D_m = 0, that is, particles freeze in the condensed phase. If once a particle enters the condensed phase, it cannot escape, then eventually all particles will end up in the condensed phase and EF=infty. The authors likely used this scheme. But as mentioned above this appears to violate the second law.

Thanks for the incisive comment. After much in-depth considerations, we are in agreement with the reviewer that Eq.1 should not be presented as a relation that is generally applicable to diffusive motions of molecules in all phase-separated systems. There are cases in which this relation can need to unphysical outcomes as correctly pointed out by the reviewer.

Nonetheless, based on our theoretical/computational modeling, it is also clear, empirically, that Eq.1 holds approximately for the NR2B/PSD system we studied, and as such it is a useful approximate relation in our analysis. We have therefore provided a plausible physical perspective for Eq.1’s applicability as an approximate relation based upon a schematic consideration of diffusion on an underlying rugged (free) energy landscape (Zhang and Chan, 2012) of a phase-separated system (See Figure 3G in the revised manuscript), while leaving further studies of such energy landscape models to future investigations.

This additional perspective is now included in the following added passage under a new subheading in the revised manuscript:

"Physical picture and a two-state, two-phase diffusion model for equilibrium and dynamic properties of PSD condensates"

(3) Despite the above two major concerns described in (1) and (2), the enrichment due to the presence of a "confined state", is reasonable. The equilibrium between "confined" and "mobile" states is determined by its interaction with the other proteins and their ratio at equilibrium corresponds to the equilibrium constant. Therefore EF=1/Pm is reasonable and comes solely from thermodynamics. In fact, the equilibrium partition between the dilute and dense phases should solely be a thermodynamic property, and therefore one may expect that it should not have anything to do with diffusivity. Can the authors please comment on this alternative interpretation?

Thanks for this thought-provoking comment. We agree with the reviewer that the relative molecular densities in the condensed versus dilute phases are governed by thermodynamics unless there is energy input into the system. However, in our formulation, the mobile ratio should not be the only parameters for determining the enrichment fold in a phase separated system. In fact, the approximate relation (Eq.1) is EF ≈ Dd/PmDm, and thus EF ≈ 1/Pm only when Dd ≈ Dm . But the speed of mobile-state diffusion in the condensed phase is found to be appreciably smaller than that of diffusion in the dilute phase (Dd > Dm). In general, a hallmark of a phase separation system is to enrich involved molecules in the condensed phase, regardless whether the molecule is a driver (or scaffold) or a client of the system. Such enrichment is expected to be resulted from the net free energy gain due to increased molecular interactions of the condensed phase (as envisioned in Response Figure 9). For example, in the phase separation systems containing PrLD-SAMME (Figure 4 of the manuscript), Pm is close to 1, but the enrichment of PrLD-SAMME in the condensed phase is much greater than 1 (estimated to be ~77, based on the fluorescence intensity of the protein in the dilute and condensed phase; Figure 5—figure supplement 1). As far as Eq.1 is concerned, this is mathematically correct because the diffusion coefficient of PrLD-SAMME in the condensed phase (D ~0.2 μm2/s) is much smaller than the diffusion coefficient of a monomeric molecule with a similar molecular mass in dilute solution (D~ 100 μm2/s, measured by FRAP-based assay; the mobility of the molecules in the dilute solution in 3D is too fast to be tracked). Physically, it’s most likely that the slower molecular motion in the condensed phase is caused by favorable intermolecular interactions and the same favorable interactions underpinning the dynamic effects lead also to a larger equilibrium Boltzmann population.

Author Response

Reviewer #1 (Public Review):

Nandan et al. attempt to demonstrate how a phenomenology in the molecular signaling network inside a cell could translate to changes in the behavior of the cell and its ability to respond/adapt to changes in the environment over time and space. While this investigation is performed in the context of mammalian cells, the result holds significance for eukaryotic cells at large and demonstrates a mechanism by which cells may use transient memory states to respond robustly to complex environmental cues. To study such mechanisms, it is important to show how the cell may encode such transient memory, how this memory is generated from environmental cues, how it translates to cellular motion, and how it enables cells to have persistent directional motion in the case of transient disruptions in the signal while responding to significant and long-lasting disruptions. The authors attempt to answer all of these questions.

Strengths:<br /> The manuscript attempts to combine mathematical theory, mechano-chemical models, numerical simulations, and experimental evidence. Thus, the investigation spans diverse methods and spatio-temporal scales (from receptors to continuum mechanical models to whole-cell motion) to answer a unified question. The mathematical theory of dynamic states and bifurcation theory provides the basis for the generation of "ghost" states that can encode transient memory; the mechano-chemical models show how such dynamical states can be realized in the EGFR signaling network; the numerical simulations show both how cells can respond to environmental cues by generating polarised states, and by navigating complex environmental cues, and experiments provide evidence that this may be the case for epithelial cells in the presence of growth factors. The manuscript is well-structured with the main conclusions clearly identified and separated from each other in the different sections. The theoretical investigation is thorough and the main text provides an intuition as to what the authors are trying to convey, while the Methods reveal the calculations performed and the approximations made. The modeling and numerical simulations are detailed and provide a baseline expectation for the system in different parameter regimes. The experiments and the analysis extensively characterize the system. I commend the authors for having delved into so many methods to answer this problem, and the authors demonstrate significant knowledge of the different methods with many novel contributions.

Weaknesses:<br /> The key weakness of the results is in establishing clear distinctions between what would be expected (naively and based on results from other groups) from alternate explanations, and what is realized in the experimental results that support the hypothesis put forward by the authors. For example, the authors quote a relatively long time scale of persistence of polarisation, but it is unclear if this is longer than is expected from slow dephosphorylation to provide evidence for the existence of the "ghost" state from the saddle-node bifurcation. Further, key experimental results regarding the persistence of motion following gradient washout seem to differ from the authors' own predictions from simulations.<br /> There are several other models that attempt to describe eukaryotic chemotactic motion that persists despite brief disruptions and is able to adapt to changes in the environment over longer timescales. In my opinion, the main strength of the paper does not lie in providing another such model, but in providing a mechanistic understanding that bridges several scales. However, this places the burden on the authors to justify the link between the different scales.<br /> This is an ambitious manuscript and the authors are clearly very bold for attempting such a comprehensive treatment of such a complex system. The authors provide an excellent framework to understand mammalian cellular chemotaxis on multiple scales and attempt to justify the framework using several experiments and extensive analysis. However, they require further analysis and characterization to demonstrate that their experimental results provide the necessary justification for their conclusions as opposed to alternate possibilities.

We thank the referee for his/her in-depth suggestions and valuable comments how to improve the manuscript, that we implemented in details in the amended version. We have especially focused on providing the necessary justification for working memory emerging from a “ghost” signaling state as opposed to slow dephosphorylation mechanism. For this, we have fitted the single-cell EGFRp temporal profiles after gradient wash-out with and without Lapatnib inhibition, with an inverse sigmoid function and quantified the respective half-life and the Hill coefficient. The analysis included in the new Figure 2 – figure supplement 2 shows that under Lapatinib treatment which inhibits the kinase activity of the receptor and thereby the dynamics of the system is guided by the dephosphorylating activity of the phosphatases, the system relaxes to the basal state in an almost exponential process (half-life ~10min., Hill coefficient ~1.3). In contrast, under normal conditions EGFR phosphorylation relaxes to the basal state in ~30min, corroborating that the system remains trapped in the “ghost” state. Moreover, the transition from the memory to the basal state is rapid, as reflected in an estimated Hill coefficient ~ 3. Additionally, we also discuss how the identified slow-time scale that emerges from the “ghost” state serves as a possible mechanistic link between the rapid phosphorylation/de-phosphorylation events and the ~40min of memory in cell shape polarization/directional cell migration after growth factor removal.

Moroever, we include additional quantification of memory in single-cell directional motility in the cases with and without EGFR inhibitor (Figure 3 – figure supplement 3), and relate these results to previously proposed mechanisms on memory in directional migration from cytoskeletal asymmetries, but also highlight the importance of memory in polarized receptor signaling as a necessary means to couple cellular processes that occur on different time-scales. We have further expanded the manuscript by providing theoretical predictions how the organization at criticality uniquely enables resolving simultaneous signals. We address the referee’s comments as outlined below:

Reviewer #2 (Public Review):

Nandan, Das et al. set out to study the mechanism by which single cells are able to follow extracellular signals in variable environments generate persistent directional migration in the presence of changing chemoattractant fields. Importantly, cells are able to (1) maintain the orientation acquired during the initial signal despite disruptions or noise while still (2) adapting migrational direction in response to newly-encountered signals. Previous models have accounted for either of these properties, but not both simultaneously. To reconcile these observations, this work proposes an underlying mechanism in which cells utilize a form of working memory.

The authors present a dynamical systems framework in which the presence of dynamical 'ghosts' in an underlying signaling network allow the cell to retain a memory of previously encountered signals. These are generated as follows: a pitchfork bifurcation confers a symmetry-breaking transition from a non-polarised to polarised signaling state/ direction-oriented cell shape. After a subsequent saddle-node bifurcation, a 'ghost' of the stable attractor emerges. This 'ghost' state is metastable, however, which is what allows cells to integrate new signals as well as to adapt their direction of migration.

The authors demonstrate these dynamics in the Epidermal Growth Factor Receptor (EGFR) signaling network. This pathway is central in many embryonic and adult processes conserved in most animal groups, making it an ideal choice to characterise a phenomenon observed in such a diverse range of cells. The authors couple a mechanical model of the cell with the biochemical signaling model for EGFR, which nicely allows them to thoroughly simulate cellular deformations that they predict will occur during polarization and motility.

Key features of the model are well-supported by empirical data from experiments: (1) quantitative live-cell imaging of polarised EGFR signaling shows the existence of a distinct polarised 'ghost' state after removal of extracellular signals and (2) motility experiments confirm the manifestation of this memory in allowing for persistent cell migration upon loss of a signal. In an extension of the latter experiment, the authors also show that cells displaying this working memory are still able to respond to changes in the chemoattractant field as necessary.

The experiments using Lapatinib to disrupt the EGFR dynamics are less convincing. The authors show that subjecting cells to this inhibitor results in the absence of memory and removes the ability of cells to maintain their orientation after the gradient was disrupted. Clarification of which aspect(s) of the EGFR network within the context of the model are precisely disrupted by Lapatinib would be helpful in strengthening the authors' claims here that it is the mechanism of working memory and not other features of the EGFR network, that is responsible for the results shown.

We thank the referee for the detailed comments and suggestions that helped us to improve the manuscript. In the amended version of the manuscript, we describe that Lapatinib hinders EGFR kinase activity, thus in the model, this will mainly affect the autocatalytic rate constant. We have performed numerical simulations where the autocatalytic rate constant is decreased after gradient removal, and show that the EGFRp temporal profile shows a slow decay after gradient removal, whereas the state-space trajectory directly transits from the polarized to the basal state without intermidate state-space trapping, thereby qualitatively resembling the experimental observations under Lapatinib treatment (compare Figure 2 – figure supplement 2C, D with Figure 2G in the amended version of the manuscript).

Reviewer #3 (Public Review):

Cell navigation in chemoattractant fields is important to many physiological processes, including in development and immunity. However, the mechanisms by which cells break symmetry to navigate up concentration gradients, while also adapting to new gradient directions, remain unclear. In this study, the authors propose a new theoretical model for this process: cells are poised near a subcritical pitchfork bifurcation, which allows them to simultaneously maintain the memory of a polarized state over intermediate timescales and respond to new cues. They show analytically that a model of EGFR phosphorylation dynamics has a subcritical pitchfork bifurcation, and use simulations of in silico cells to demonstrate both memory and adaptability in this system. They further measure EGFR phosphorylation profiles, as well as migration tracks under external gradients, in real cells.

This work contributes an interesting new theoretical framework, bolstered by substantial analysis and simulations, as well as valuable measurements of cell behavior and polarization. Both the modeling and the measurements are careful and thorough, and each represents a substantial contribution to decoding the complex problem of cell navigation. The measurements support and quantify the phenomenon of directional memory. The main weakness is that it is not clear that they also support the mechanism proposed by the model.

Theoretical framework

One of the main strengths of this work is the thorough theoretical analysis of a model of symmetry breaking in EGFR phosphorylation. The authors perform linear stability analysis and a weakly nonlinear amplitude equation analysis to characterize the transition. Additionally, they convincingly demonstrate in simulations that this model can generate robust polarization, with memory over intermediate timescales and responsiveness to new gradient directions. However, the relationship between the full dynamical system and the bifurcation diagrams shown in Figure 1A and Figure 1-Figure Supplement 1B is not clear. In particular, there is an implicit reduction from an infinite dimensional system (continuous in space) to an ODE system.<br /> From Methods 5.15, it appears that this was accomplished by approximating the continuous cell perimeter as a diffusively-coupled two-component system, representing the left and right halves of the cell (Methods 5.15 Equation 18 to Equation 19). However, this is not stated explicitly in the methods, and not at all in the main text, making the argument difficult to follow. Additionally, the main text and methods describe the emergence of an unstable odd spatial eigenmode as the key requirement for the pitchfork bifurcation. It is not clear why it is sufficient to show this emergence in the two-component system.

We thank the referee for the detailed and insightful comments which we implemented in details in the amended version of the manuscript. Indeed, as the referee commented, we have assumed a simplified one-dimensional geometry composed of two compartments (front and back), resembling a projection of the membrane along the main diagonal of the cell. The standard approach of modeling the diffusion along the membrane in this case is simple exchange of the diffusing components. The one-dimensional projection, as demonstrated in the analysis, preserves all of the main features of the PDE model. The numerical bifurcation analysis was only performed for comparative purposes. In the amended version of the manuscript we thus extend the description of this simplification, as well as the purpose of its implementation. Additionally, one of the reasons for developing the theoretical network for us was to provide a method how subcritical PB can be identified in general in PDE models.

The schematic of the bifurcation in Figure 1A / now in Figure 1 – figure supplement 1A, as well as the numerical bifurcation analysis of the EGFR model in Figure 1-Supplement 1C represent a subcritical pitchfork bifurcation, but the alignment of IHSS branches is slightly different in the EGFR model. This however has no influence on the full dynamics of the system, or the proposed hypothesis. Moreover, in order to explain in details the dynamical transitions - how the unfolding of the PB results in robust polarization and how the organization at criticality enables temporal memory in polarization to be maintained, we included a revised schematic in Figure1 – figure supplement 1A that shows the signal induced transitions that were previously depicted in a compact way in Figure1A, and included respective description in Methods, Section 5.15. The corresponding transitions for the one-dimensional projection EGFR model is also included in the detailed response (Figure 2) for comparison.

Relationship between the measurements and model

The second main strength of this work is the contribution of controlled measurements of cell motility, polarization, and phosphorylated EGFR profiles. The measurements of cell migration presented here support the claim that the cells have a memory of past gradients. Additionally, the authors contribute very nice quantifications of the memory timescale. The Lapatinib experiments also support the claim that this memory is related to EGFR activity. However, there are a number of ways in which the real cells appear not to behave like the in silico cells. Polarization in phosphorylated EGFR is present only some of the time in the data, and if present, appears to be weak and/or variable, in magnitude and direction (phosphorylated EGFR profiles, figure 2C, Figure 2-Figure supplement 1D, E). Even for the subset of cells that display polarized EGFR phosphorylation profiles, the average profile is shown after aligning to the peak for each cell (Figure 2-Figure Supplement 1C), so it is not clear that they polarize in the direction of the gradient.

We thank the referee for these comments which we used as a basis to improve the presentation of the results in the amended version of the manuscript. In order to demonstrate that cells polarize in the direction of the maximal EGF concentration, we have used the EGF647 intensity to quantify the growth factor distribution around each cell and calculated the angle between the maximum of the EGF647 distribution and projection of EGFRp spatial distribution (summarized in Figure 2 – figure supplement 1F and Methods). In brief, for quantification of EGF647 distribution outside each cell, the cell masks were extended by 23 pixels, and the outer rim of 15 pixels was used for the quantification. A radial histogram of the obtained angles confirms that the polarization of EGFRp is in the direction of maximal EGF647, with the variability arising from the positioning of the cells within the gradient chamber. That cells polarize in direction of the gradient can be indirectly inferred also from the migration data (Fig. 3C), where we have estimated the projection of the relative displacement angles with respect to the gradient direction. The cos 𝜃 values during and for ~50min after gradient removal are maintained around 1 (cells migrate in direction of the gradient), before re-setting to 0, which is characteristic for the no-stimulus case.

The length of the memory in EGFRp polarization is indeed variable in single cells, being on average ~40-50min. The length of the memory is directly related to the total EGFR concentration on the plasma membrane – the closer EGFRt is to the value for which the SNPB is exhibited, the longer the duration of the memory is, and in theory

𝑀𝑒𝑚𝑜𝑟𝑦 𝑑𝑢𝑟𝑎𝑡𝑖𝑜𝑛 ∝ 𝐸𝐺𝐹𝑅𝑡1/2. From the experimental measurments we have indeed observed a correlation between these two quantities, which we include here for the referee’s perusal (Figure 1). However, direct fitting to the experimental data with the given dependency could not be performed because of the following reasons: In general, the fitting function is 𝑓(𝐸𝐺𝐹𝑅𝑇) = 𝑐 ∗ (𝑐𝐸𝐺𝐹𝑅𝑇,𝑆𝑁−𝐸𝐺𝐹𝑅𝑇)n, where c= const. and 𝑐𝐸𝐺𝐹𝑅𝑇,𝑆𝑁 is the total EGFR concentration at the plasma membrane that marks the position of the SNPB. This value however cannot be identified with certainty from the experiments. Thus, we have chosen a fixed value based on the spread of the data and in this case, the fitting resulted to n = 0.49, which approximates well the theoretical value. However, since one of the parameters must be arbitrarily chose, we refrain from presenting the fit.

*Figure 1: Correlation between single-cell transient memory duration and plasma membrane abundance of 𝐸𝐺𝐹𝑅𝑚𝐶𝑖𝑡𝑟𝑖𝑛𝑒. *

The real cells also appear to track the gradient far less reliably than the in silico cells (e.g. Figure 4B vs. 4C). Thus the measurements demonstrate and quantify the phenomenon of directional memory, but it is not clear that they support the mechanism proposed by the model, i.e. a symmetry-breaking transition in phosphorylated EGFR.

We would like to emphasize here that the symmetry-breaking transition via a subcritical pitchfork bifurcation gives rise to robust polarization in the direction of the growth factor signal, whereas critical organization at the SNPB – temporal memory of the polarized state, as well as capability for integration of signals that change both over time and space. The analytical as well as the numerical analysis of the experimentally identified EGFR network verifies that this network exhibits a subcritical PB. In the amended version of the manuscript, we have also included quantification of the directionality of polarization (Figure 2 – figure supplement 1F).

We would like to note however, that the difference between the simulations and the experiments in Figure 4 lies in the fact that the directional migration in the physical model of the cell, due to the complexity of connecting the signaling with the physical model, is realized as a ballistic movement, whereas experimentally we have identified that cells perform persistent biased random walk (Figure 3D). In the amended version of the manuscript we have discussed these differences in relation to Fig.4.

Moreover, in the experiments, the EGF647 gradient is established from the top of the microfluidic chamber, and therefore there will be variability due to the position of cells within the chamber, the disruption of the gradient due to the presence of neighboring cells etc. The single cell trajectories (several examples shown in Figure 4 – figure supplement 1F) and the quantification of the relative displacement angles (Figure 4D,E) however clearly depict that cells migrate in the gradient direction and rapidly adapt to the changes in the external cues.

Additionally, in the authors' model, the features of memory and adaptability in cell navigation depend on the system being poised near a critical point. Thus, in silico, the sensing system 'breaks' when the system parameters are moved away from this point. In particular, cells with increased receptor concentration on their surface cannot adapt to new gradient directions (Section 1, final paragraph; Figure 1-Figure Supplement 1E-G). Based on this, the authors' theoretical framework makes a nonintuitive prediction: overexpression of the surface receptor EGFR in real cells should render them insensitive to changes in the concentration gradient. The fact that the model suggests a surprising, testable prediction is a strength of the framework. A weakness is that the consistency of this prediction with empirical data is not discussed (though the authors note similarities between this regime and unrealistic features of previous models).

The organization at criticality is indeed dependent on the total concentration of receptors at the plasma membrane. The trafficking of the epidermal growth factor receptors has been previously characterized in details and demonstrated that the ligandless receptors continuously recycle to the plasma membrane, whereas the ligandbound receptors are unidirectionally removed and are trafficked to the lysosome where they await degradation [5]. Thus, how quickly the system will move away from criticality depends directly on the dose and the duration of the EGF stimulus, as this is directly proportional to the fraction of liganded receptors; whereas re-setting of the system at criticality will be afterwards depended on the time scale for biosynthesis of new receptors [17].<br /> Overexpression of EGFR receptors will cause the system to display either permanent polarization (organization in the stable IHSS state) or uniform activation (high HSS branch). We have tested numerically the features of the system when it displays permanent memory (Figure 4 – figure supplement 1C,D) and demonstrated that in this case, cells are not able to resolve signals from opposite directions and therefore migration will be halted. Additionally we also now tested numerically the capability of the cells for resolving simultaneous signals with different amplitudes from opposite direction, and demonstrate that permanent memory as resulting from receptor organization hinders the cells in this comparison task, in contrast to organization at criticality (Figure 4 – figure supplement 2). In the amended version of the manuscript we included a discussion of these points raised by the referee and hope that this allows for more clear presentation of our findings and their implications.

Author Response

Reviewer #1 (Public Review):

The authors set out to extend modeling of bispecific engager pharmacology through explicit modelling of the search of T cells for tumour cells, the formation of an immunological synapse and the dissociation of the immunological synapse to enable serial killing. These features have not been included in prior models and their incorporation may improve the predictive value of the model.

Thank you for the positive feedback.

The model provides a number of predictions that are of potential interest- that loss of CD19, the target antigen, to 1/20th of its initial expression will lead to escape and that the bone marrow is a site where the tumour cells may have the best opportunity to develop loss variants due to the limited pressure from T cells.

Thank you for the positive feedback.

A limitation of the model is that adhesion is only treated as a 2D implementation of the blinatumomab mediated bridge between T cell and B cells- there is no distinct parameter related to the distinct adhesion systems that are critical for immunological synapse formation. For example, CD58 loss from tumours is correlated with escape, but it is not related to the target, CD19. While they begin to consider the immunological synapse, they don't incorporate adhesion as distinct from the engager, which is almost certainly important.

We agree that adhesion molecules play critical roles in cell-cell interaction. In our model, we assumed these adhesion molecules are constant (or not showing difference across cell populations). This assumption made us to focus on the BiTE-mediated interactions.

Revision: To clarify this point, we added a couple of sentences in the manuscript.

“Adhesion molecules such as CD2-CD58, integrins and selectins, are critical for cell-cell interaction. The model did not consider specific roles played by these adhesion molecules, which were assumed constant across cell populations. The model performed well under this simplifying assumption”.

In addition, we acknowledged the fact that “synapse formation is a set of precisely orchestrated molecular and cellular interactions. Our model merely investigated the components relevant to BiTE pharmacologic action and can only serve as a simplified representation of this process”.

While the random search is a good first approximation, T cell behaviour is actually guided by stroma and extracellular matrix, which are non-isotropic. In a lymphoid tissue the stroma is optimised for a search that can be approximated as brownian, or more accurately, a correlated random walk, but in other tissues, particularly tumours, the Brownian search is not a good approximation and other models have been applied. It would be interesting to look at observations from bone marrow or other sites to determine the best approximating for the search related to BiTE targets.

We agree that the tissue stromal factors greatly influence the patterns of T cell searching strategy. Our current model considered Brownian motion as a good first approximation for two reasons: 1) we define tissues as homogeneous compartments to attain unbiased evaluations of factors that influence BiTE-mediated cell-cell interaction, such as T cell infiltration, T: B ratio, and target expression. The stromal factors were not considered in the model, as they require spatially resolved tissue compartments to represent the gradients of stromal factors; 2) our model was primarily calibrated against in vitro data obtained from a “well-mixed” system that does not recapitulate specific considerations of tissue stromal factors. We did not obtain tissue-specific data to support the prediction of T cell movement. This is under current investigation in our lab. Therefore, we are cautious about assuming different patterns of T cell movement in the model when translating into in vivo settings. We acknowledged the limitation of our model for not considering the more physiologically relevant T-cell searching strategies.

Revision: In the Discussion, we added a limitation of our model: “We assumed Brownian motion in the model as a good first approximation of T cell movement. However, T cells often take other more physiologically relevant searching strategies closely associated with many stromal factors. Because of these stromal factors, the cell-cell encounter probabilities would differ across anatomical sites.”

Reviewer #3 (Public Review):

Liu et al. combined mechanistic modeling with in vitro experiments and data from a clinical trial to develop an in silico model to describe response of T cells against tumor cells when bi-specific T cell engager (BiTE) antigens, a standard immunotherapeutic drug, are introduced into the system. The model predicted responses of T cell and target cell populations in vitro and in vivo in the presence of BiTEs where the model linked molecular level interactions between BiTE molecules, CD3 receptors, and CD19 receptors to the population kinetics of the tumor and the T- cells. Furthermore, the model predicted tumor killing kinetics in patients and offered suggestions for optimal dosing strategies in patients undergoing BiTE immunotherapy. The conclusions drawn from this combined approach are interesting and are supported by experiments and modeling reasonably well. However, the conclusions can be tightened further by making some moderate to minor changes in their approach. In addition, there are several limitations in the model which deserves some discussion.

Strengths

A major strength of this work is the ability of the model to integrate processes from the molecular scales to the populations of T cells, target cells, and the BiTE antibodies across different organs. A model of this scope has to contain many approximations and thus the model should be validated with experiments. The authors did an excellent job in comparing the basic and the in vitro aspects of their approach with in vitro data, where they compared the numbers of engaged target cells with T cells as the numbers of the BiTE molecules, the ratio of effector and target cells, and the expressions of the CD3 and CD19 receptors were varied. The agreement with the model with the data were excellent in most cases which led to several mechanistic conclusions. In particular, the study found that target cells with lower CD19 expressions escape the T cell killing.

The in vivo extension of the model showed reasonable agreements with the kinetics of B cell populations in patients where the data were obtained from a published clinical trial. The model explained differences in B cell population kinetics between responders and non-responders and found that the differences were driven by the differences in the T cell numbers between the groups. The ability of the model to describe the in vivo kinetics is promising. In addition, the model leads to some interesting conclusions, e.g., the model shows that the bone marrow harbors tumor growth during the BiTE treatment. The authors then used the model to propose an alternate dosage scheme for BiTEs that needed a smaller dose of the drug.

Thank you for the positive comments.

Weaknesses

There are several weaknesses in the development of the model. Multiscale models of this nature contain parameters that need to be estimated by fitting the model with data. Some these parameters are associated with model approximations or not measured in experiments. Thus, a common practice is to estimate parameters with some 'training data' and then test model predictions using 'test data'. Though Supplementary file 1 provides values for some of the parameters that appeared to be estimated, it was not clear which dataset were used for training and which for test. The confidence intervals of the estimated parameters and the sensitivity of the proposed in vivo dosage schemes to parameter variations were unclear.

We agree with the reviewer on the model validation.

Revision: To ensure reproducibility, we summarized model assumptions and parameter values/sources in the supplementary file 1. To mimic tumor heterogeneity and evolution process, we applied stochastic agent-based models, which are challenging to be globally optimized against the data. The majority of key parameters was obtained or derived from the literature. Details have been provided in the response to Reviewer 3 - Question 1. In our modeling process, we manually optimized sensitive coefficient (β) for base model using pilot in-vitro data and sensitive coefficient (β) for in-vivo model by re-calibrating against the in-vitro data at a low BiTE concentration. BiTE concentrations in patients (mostly < 2 ng/ml) is only relevant to the low bound of the concentration range we investigated in vitro (0.65-2000 ng/ml). We have added some clarification/limitation of this approach in the text (details are provided in the following question). We understand the concerns, but the agent-based modeling nature prevent us to do global optimization.

The model appears to show few unreasonable behaviors and does not agree with experiments in several cases which could point to missing mechanisms in the model. Here are some examples. The model shows a surprising decrease in the T cell-target cell synapse formation when the affinity of the BiTEs to CD3 was increased; the opposite should have been more intuitive. The authors suggest degradation of CD3 could be a reason for this behavior. However, this probably could be easily tested by removing CD3 degradation in the model. Another example is the increase in the % of engaged effector cells in the model with increasing CD3 expressions does not agree well with experiments (Fig. 3d), however, a similar fold increase in the % of engaged effector cells in the model agrees better with experiments for increasing CD19 expressions (Fig. 3e). It is unclear how this can be explained given CD3 and CD19 appears to be present in similar copy numbers per cell (~104 molecules/cell), and both receptors bind the BiTE with high affinities (e.g., koff < 10-4 s-1).

Thank you for pointing this out. The bidirectional effect of CD3 affinity on IS formation is counterintuitive. In a hypothetical situation when there is no CD3 downregulation, the bidirectional effect disappears (as shown below), consistent with our view that CD3 downregulation accounts for the counterintuitive behavior. We have included the simulation to support our point. From a conceptual standpoint, the inclusion of CD3 degradation means the way to maximize synapse formation is for the BiTE to first bind tumor antigen, after which the tumor-BiTE complex “recruits” a T cell through the CD3 arm.

We agree that the model did not adequately capture the effect of CD3 expression at the highest BiTE concentration 100 ng/ml, while the effects at other BiTE concentrations were well captured (as shown below, left). The model predicted a much moderate effect of CD3 expression on IS formation at the highest concentration. This is partly because the model assumed rapid CD3 downregulation upon antibody engagement. We did a similar simulation as above, with moderate CD3 downregulation (as shown below, right). This increases the effect of CD3 expression at the highest BiTE concentration, consistent with experiments. Interestingly, a rapid CD3 downregulation rate, as we concluded, is required to capture data profiles at all other conditions. Considering BiTE concentration at 100 ng/ml is much higher than therapeutically relevant level in circulation (< 2 ng/ml), we did not investigate the mechanism underlying this inconsistent model prediction but we acknowledged the fact that the model under-predicted IS formation in Figure 3d. Notably, this discrepancy may rarely appear in our clinical predictions as the CD3 expression is low level and blood BiTE concentration is very low (< 2 ng/ml).

Revision: we have made text adjustment to increase clarity on these points. In addition, we added: “The base model underpredicted the effect of CD3 expression on IS formation at 100 ng/ml BiTE concentration, which is partially because of the rapid CD3 downregulation upon BiTE engagement and assay variation across experimental conditions.”

The model does not include signaling and activation of T cells as they form the immunological synapse (IS) with target cells. The formation IS leads to aggregation of different receptors, adhesion molecules, and kinases which modulate signaling and activation. Thus, it is likely the variations of the copy numbers of CD3, and the CD19-BiTE-CD3 will lead to variations in the cytotoxic responses and presumably to CD3 degradation as well. Perhaps some of these missing processes are responsible for the disagreements between the model and the data shown in Fig. 3. In addition, the in vivo model does not contain any development of the T cells as they are stimulated by the BiTEs. The differences in development of T cells, such as generation of dysfunctional/exhausted T cells could lead to the differences in responses to BiTEs in patients. In particular, the in vivo model does not agree with the kinetics of B cells after day 29 in non-responders (Fig. 6d); could the kinetics of T cell development play a role in this?

We agree that intracellular signaling is critical to T cell activation and cytotoxic effects. IS formation, T cell activation, and cytotoxicity are a cascade of events with highly coordinated molecular and cellular interactions. Compared to the events of T cell activation and cytotoxicity, IS formation occurs at a relatively earlier time. As shown in our study, IS formation can occur at 2-5 min, while the other events often need hours to be observed. We found that IS formation is primarily driven by two intercellular processes: cell-cell encounter and cell-cell adhesion. The intracellular signaling would be initiated in the process of cell-cell adhesion or at the late stage of IS formation. We think these intracellular events are relevant but may not be the reason why our model did not adequately capture the profiles in Figure 3d at the highest BiTE concentrations. Therefore, we did not include intracellular signaling in the models. Another reason was that we simulated our models at an agent level to mimic the process of tumor evolution, which is computationally demanding. Intracellular events for each cell may make it more challenging computationally.

T cell activation and exhaustion throughout the BiTE treatment is very complicated, time-variant and impacted by multiple factors like T cell status, tumor burden, BiTE concentration, immune checkpoints, and tumor environment. T cell proliferation and death rates are challenging to estimate, as the quantitative relationship with those factors is unknown. Therefore, T cell abundance (expansion) was considered as an independent variable in our model. T cell counts are measured in BiTE clinical trials. We included these data in our model to reveal expanded T cell population. Patients with high T cell expansion are often those with better clinical response. Notably, the T cell decline due to rapid redistribution after administration was excluded in the model. T cell abundance was included in the simulations in Figure 6 but not proof of concept simulations in Figure 7.

In Figure 6d, kinetics of T cell abundance had been included in the simulations for responders and non-responders in MT103-211 study. Thus, the kinetics of T cell development can’t be used to explain the disagreement between model prediction and observation after day 29 in non-responders. The observed data is actually median values of B-cell kinetics in non-responders (N = 27) with very large inter-subject variation (baseline from 10-10000/μL), which makes it very challenging to be perfectly captured by the model. A lot of non-responders with severe progression dropped out of the treatment at the end of cycle 1, which resulted in a “more potent” efficacy in the 2nd cycle. This might be main reason for the disagreement.

Variation in cytotoxic response was not included in our models. Tumor cells were assumed to be eradicated after the engagement with effecter cells, no killing rate or killing probability was implemented. This assumption reduced the model complexity and aligned well with our in-vitro and clinical data. Cytotoxic response in vivo is impacted by multiple factors like copy number of CD3, cytokine/chemokine release, tumor microenvironment and T cell activation/exhaustion. For example, the cytotoxic response and killing rate mediated by 1:1 synapse (ET) and other variants (ETE, TET, ETEE, etc.) are supposed to be different as well. Our model did not differentiate the killing rate of these synapse variants, but the model has quantified these synapse variants, providing a framework for us to address these questions in the future. We agree that differentiate the cytotoxic responses under different scenarios cell may improve model prediction and more explorations need to be done in the future.

Revision: We added a discussion of the limitations which we believe is informative to future studies.

“Our models did not include intracellular signaling processes, which are critical for T activation and cytotoxicity. However, our data suggests that encounter and adhesion are more relevant to initial IS formation. To make more clinically relevant predictions, the models should consider these intracellular signaling events that drive T cell activation and cytotoxic effects. Of note, we did consider the T cell expansion dynamics in organs as independent variable during treatment for the simulations in Figure 6. T cell expansion in our model is case-specific and time-varying.”

References:

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Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors present a new technique for analysing low complexity regions (LCRs) in proteins- extended stretches of amino acids made up from a small number of distinct residue types. They validate their new approach against a single protein, compare this technique to existing methods, and go on to apply this to the proteomes of several model systems. In this work, they aim to show links between specific LCRs and biological function and subcellular location, and then study conservation in LCRs amongst higher species.

The new method presented is straightforward and clearly described, generating comparable results with existing techniques. The technique can be easily applied to new problems and the authors have made code available.

This paper is less successful in drawing links between their results and the importance biologically. The introduction does not clearly position this work in the context of previous literature, using relatively specialised technical terms without defining them, and leaving the reader unclear about how the results have advanced the field. In terms of their results, the authors further propose interesting links between LCRs and function. However, their analyses for these most exciting results rely heavily on UMAP visualisation and the use of tests with apparently small effect sizes. This is a weakness throughout the paper and reduces the support for strong conclusions.

We appreciate the reviewer’s comments on our manuscript. To address comments about the clarity of the introduction and the position of our findings with respect to the rest of the field, we have made several changes to the text. We have reworked the introduction to provide a clearer view of the current state of the LCR field, and our goals for this manuscript. We also have made several changes to the beginnings and ends of several sections in the Results to explicitly state how each section and its findings help advance the goal we describe in the introduction, and the field more generally. We hope that these changes help make the flow of the paper more clear to the reader, and provide a clear connection between our work and the field.

We address comments about the use of UMAPs and statistical tests in our responses to the specific comments below.

Additionally, whilst the experimental work is interesting and concerns LCRs, it does not clearly fit into the rest of the body of work focused as it is on a single protein and the importance of its LCRs. It arguably serves as a validation of the method, but if that is the author's intention it needs to be made more clearly as it appears orthogonal to the overall drive of the paper.

In response to this comment, we have made more explicit the rationale for choosing this protein at the beginning of this section, and clarify the role that these experiments play in the overall flow of the paper.

Our intention with the experiments in Figure 2 was to highlight the utility of our approach in understanding how LCR type and copy number influence protein function. Understanding how LCR type and copy number can influence protein function is clearly outlined as a goal of the paper in the Introduction.

In the text corresponding to Figure 2, we hypothesize how different LCR relationships may inform the function of the proteins that have them, and how each group in Figure 2A/B can be used to test these hypotheses. The global view provided by our method allows proteins to be selected on the basis of their LCR type and copy number for further study.

To demonstrate the utility of this view, we select a key nucleolar protein with multiple copies of the same LCR type (RPA43, a subunit of RNA Pol I), and learn important features driving its higher-order assembly in vivo and in vitro. We learned that in vivo, a least two copies of RPA43’s K-rich LCRs are required for nucleolar integration, and that these K-rich LCRs are also necessary for in vitro phase separation.

Despite this protein being a single example, we were able to gain important insights about how K-rich LCR copy number affects protein function, and that both in vitro higher order assembly and in vivo nucleolar integration can be explained by LCR copy number. We believe this opens the door to ask further questions about LCR type and copy number for other proteins using this line of reasoning.

Overall I think the ideas presented in the work are interesting, the method is sound, but the data does not clearly support the drawing of strong conclusions. The weakness in the conclusions and the poor description of the wider background lead me to question the impact of this work on the broader field.

For all the points where Reviewer #1 comments on the data and its conclusions, we provide explanations and additional analyses in our responses below showing that the data do indeed support our conclusions. In regards to our description of the wider background, we have reworked our introduction to more clearly link our work to the broader field, such that a more general audience can appreciate the impact of our work.

Technical weaknesses

In the testing of the dotplot based method, the manuscript presents a FDR rate based on a comparison between real proteome data and a null proteome. This is a sensible approach, but their choice of a uniform random distribution would be expected to mislead. This is because if the distribution is non-uniform, stretches of the most frequent amino will occur more frequently than in the uniform distribution.

Thank you for pointing this out. The choice of null proteome was a topic of much discussion between the authors as this work was being performed. While we maintain that the uniform background is the most appropriate, the question from this reviewer and the other reviewers made us realize that a thorough explanation was warranted. For a complete explanation for our choice of this uniform null model, please see the newly added appendix section, Appendix 1.

The authors would also like to point out that the original SEG algorithm (Wootton and Federhen, 1993) also made the intentional choice of using a uniform background model.

More generally I think the results presented suggest that the results dotplot generates are comparable to existing methods, not better and the text would be more accurate if this conclusion was clearer, in the absence of an additional set of data that could be used as a "ground truth".

We did not intend to make any strong claims about the relative performance of our approach vs. existing methods with regard to the sequence entropy of the called LCRs beyond them being comparable, as this was not the main focus of our paper. To clarify the text such that it reflects this, we have removed ‘or better’ from the text in this section.

The authors draw links between protein localisation/function and LCR content. This is done through the use of UMAP visualisation and wilcoxon rank sum tests on the amino acid frequency in different localisations. This is convincing in the case of ECM data, but the arguments are substantially less clear for other localisations/functions. The UMAP graphics show generally that the specific functions are sparsely spread. Moreover when considering the sample size (in the context of the whole proteome) the p-value threshold obscures what appear to be relatively small effect sizes.

We would first like to note that some of the amino acid frequency biases have been documented and experimentally validated by other groups, as we write and reference in the manuscript. Nonetheless, we have considered the reviewer's concerns, and upon rereading the section corresponding to Figure 3, we realize that our wording may have caused confusion in the interpretation there. In addition to clarifying this in the manuscript, we believe the following clarification may help in the interpretations drawn from that section.

Each point in this analysis (and on the UMAP) is an LCR from a protein, and as such multiple LCRs from the same protein will appear as multiple points. This is particularly relevant for considering the interpretation of the functional/higher order assembly annotations because it is not expected that for a given protein, all of the LCRs will be directly relevant to the function/annotation. Just because proteins of an assembly are enriched for a given type of LCR does not mean that they only have that kind of LCR. In addition to the enriched LCR, they may or may not have other LCRs that play other roles.

For example, a protein in the Nuclear Speckle may contain both an R/S-rich LCR and a Q-rich LCR. When looking at the Speckle, all of the LCRs of a protein are assigned this annotation, and so such a protein would contribute a point in the R/S region as well as elsewhere on the map. Because such "non-enriched" LCRs do not occur as frequently, and may not be relevant to Speckle function, they are sparsely spread.

We have now changed the wording in that section of the main text to reflect that the expectation is not all LCRs mapping to a certain region, but enrichment of certain LCR compositions.

Reviewer #3 (Public Review):

The authors present a systematic assessment of low complexity sequences (LCRs) apply the dotplot matrix method for sequence comparison to identify low-complexity regions based on per-residue similarity. By taking the resulting self-comparison matrices and leveraging tools from image processing, the authors define LCRs based on similarity or non-similarity to one another. Taking the composition of these LCRs, the authors then compare how distinct regions of LCR sequence space compare across different proteomes.

The paper is well-written and easy to follow, and the results are consistent with prior work. The figures and data are presented in an extremely accessible way and the conclusions seem logical and sound.

My big picture concern stems from one that is perhaps challenging to evaluate, but it is not really clear to me exactly what we learn here. The authors do a fine job of cataloging LCRs, offer a number of anecdotal inferences and observations are made - perhaps this is sufficient in terms of novelty and interest, but if anyone takes a proteome and identifies sequences based on some set of features that sit in the tails of the feature distribution, they can similarly construct intriguing but somewhat speculative hypotheses regarding the possible origins or meaning of those features.

The authors use the lysine-repeats as specific examples where they test a hypothesis, which is good, but the importance of lysine repeats in driving nucleolar localization is well established at this point - i.e. to me at least the bioinformatics analysis that precedes those results is unnecessary to have made the resulting prediction. Similarly, the authors find compositional biases in LCR proteins that are found in certain organelles, but those biases are also already established. These are not strictly criticisms, in that it's good that established patterns are found with this method, but I suppose my concern is that this is a lot of work that perhaps does not really push the needle particularly far.

As an important caveat to this somewhat muted reception, I recognize that having worked on problems in this area for 10+ years I may also be displaying my own biases, and perhaps things that are "already established" warrant repeating with a new approach and a new light. As such, this particular criticism may well be one that can and should be ignored.

We thank the reviewer for taking the time to read and give feedback for our manuscript. We respectfully disagree that our work does not push the needle particularly far.

In the section titled ‘LCR copy number impacts protein function’, our goal is not to highlight the importance of lysines in nucleolar localization, but to provide a specific example of how studying LCR copy number, made possible by our approach, can provide specific biological insights. We first show that K-rich LCRs can mediate in vitro assembly. Moreover, we show that the copy number of K-rich LCRs is important for both higher order assembly in vitro and nucleolar localization in cells, which suggests that by mediating interactions, K-rich LCRs may contribute to the assembly of the nucleolus, and that this is related to nucleolar localization. The ability of our approach to relate previously unrelated roles of K-rich LCRs not only demonstrates the value of a unified view of LCRs but also opens the door to study LCR relationships in any context.

Furthermore, our goal in identifying established biases in LCR composition for certain assemblies was to validate that the sequence space captures higher order assemblies which are known. In addition to known biases, we use our approach to uncover the roles of LCR biases that have not been explored (e.g. E-rich LCRs in nucleoli, see Figure 4 in revised manuscript), and discover new regions of LCR sequence space which have signatures of higher order assemblies (e.g. Teleost-specific T/H-rich LCRs). Collectively, our results show that a unified view of LCRs relates the disparate functions of LCRs.

In response to these comments, we have added additional explanations at the end of several sections to clarify the impact of our findings in the scope of the broader field. Furthermore, as we note in our main response, we have added experimental data with new findings to address this concern.

That overall concern notwithstanding, I had several other questions that sprung to mind.

Dotplot matrix approach

The authors do a fantastic job of explaining this, but I'm left wondering, if one used an algorithm like (say) SEG, defined LCRs, and then compared between LCRs based on composition, would we expect the results to be so different? i.e. the authors make a big deal about the dotplot matrix approach enabling comparison of LCR type, but, it's not clear to me that this is just because it combines a two-step operation into a one-step operation. It would be useful I think to perform a similar analysis as is done later on using SEG and ask if the same UMAP structure appears (and discuss if yes/no).

Thank you for your thoughtful question about the differences between SEG and the dotplot matrix approach. We have tried our best to convey the advantages of the dotplot approach over SEG in the paper, but we did not focus on this for the following reasons:

1) SEG and dotplot matrices are long-established approaches to assessing LCRs. We did not see it in the scope of our paper to compare between these when our main claim is that the approach as a whole (looking at LCR sequence, relationships, features, and functions) is what gives a broader understanding of LCRs across proteomes. The key benefits of dotplots, such as direct visual interpretation, distinguishing LCR types and copy number within a protein, are conveyed in Figure 1A-C and Figure 1 - figure supplements 1 and 4. In fact, these benefits of dotplots were acknowledged in the early SEG papers, where they recommended using dotplots to gain a prior understanding of protein sequences of interest, when it was not yet computationally feasible to analyze dotplots on the same scale as SEG (Wootton and Federhen, Methods in Enzymology, vol. 266, 1996, Pages 554-571). Thus, our focus is on the ability to utilize image processing tools to "convert" the intuition of dotplots into precise read-out of LCRs and their relationships on a multi-proteome scale. All that being said, we have considered differences between these methods as you can see from our technical considerations in part 2 below.

2) SEG takes an approach to find LCRs irrespective of the type of LCR, primarily because SEG was originally used to mask LCR-containing regions in proteins to facilitate studies of globular domains. Because of this, the recommended usage of SEG commonly fuses nearby LCRs and designates the entire region as "low complexity". For the original purpose of SEG, this is understandable because it takes a very conservative approach to ensure that the non-low complexity regions (i.e. putative folded domains) are well-annotated. However, for the purpose of distinguishing LCR composition, this is not ideal because it is not stringent in separating LCRs that are close together, but different in composition. Fusion can be seen in the comparison of specific LCR calls of the collagen CO1A1 (Figure 1 - figure supplement 3E), where even the intermediate stringency SEG settings fuse LCR calls that the dotplot approach keeps separate. Finally, we did also try downstream UMAP analysis with LCRs called from SEG, and found that although certain aspects of the dotplot-based LCR UMAP are reflected in the SEG-based LCR UMAP, there is overall worse resolution with default settings, which is likely due to fused LCRs of different compositions. Attempting to improve resolution using more stringent settings comes at the cost of the number of LCRs assessed. We have attached this analysis to our rebuttal for the reviewer, but maintain that this comparison is not really the focus of our manuscript. We do not make strong claims about the dotplot matrices being better at calling LCRs than SEG, or any other method.

UMAPs generated from LCRs called by SEG

LCRs from repeat expansions

I did not see any discussion on the role that repeat expansions can play in defining LCRs. This seems like an important area that should be considered, especially if we expect certain LCRs to appear more frequently due to a combination of slippy codons and minimal impact due to the biochemical properties of the resulting LCR. The authors pursue a (very reasonable) model in which LCRs are functional and important, but it seems the alternative (that LCRs are simply an unavoidable product of large proteomes and emerge through genetic events that are insufficiently deleterious to be selected against). Some discussion on this would be helpful. it also makes me wonder if the authors' null proteome model is the "right" model, although I would also say developing an accurate and reasonable null model that accounts for repeat expansions is beyond what I would consider the scope of this paper.

While the role of repeat expansions in generating LCRs has been studied and discussed extensively in the LCR field, we decided to focus on the question of which LCRs exist in the proteome, and what may be the function downstream of that. The rationale for this is that while one might not expect a functional LCR to arise from repeat expansion, this argument is less of a concern in the presence of evidence that these LCRs are functional. For example, for many of these LCRs (e.g. a K-rich LCR, R/S-rich LCR, etc as in Figure 3), we know that it is sufficient for the integration of that sequence into the higher order assembly. Moreover, in more recent cases, variation of the length of an LCR was shown to have functional consequences (Basu et al., Cell, 2020), suggesting that LCR emergence through repeat expansions does not imply lack of function. Therefore, while we think the origin of a LCR is an interesting question, whether or not that LCR was gained through repeat expansions does not fall into the scope of this paper.

In regards to repeat expansions as it pertains to our choice of null model, we reasoned that because the origin of an LCR is not necessarily coupled to its function, it would be more useful to retain LCR sequences even if they may be more likely to occur given a background proteome composition. This way, instead of being tossed based on an assumption, LCRs can be evaluated on their function through other approaches which do not assume that likelihood of occurrence inversely relates to function.

While we maintain that the uniform background is the most appropriate, the question from this reviewer and the other reviewers made us realize that a thorough explanation was warranted for this choice of null proteome. For a complete explanation for our choice of this uniform null model, please see the newly added appendix section, Appendix 1.

The authors would also like to point out that the original SEG algorithm (Wootton and Federhen, 1993) also made the intentional choice of using a uniform background model.

Minor points

Early on the authors discuss the roles of LCRs in higher-order assemblies. They then make reference to the lysine tracts as having a valence of 2 or 3. It is possibly useful to mention that valence reflects the number of simultaneous partners that a protein can interact with - while it is certainly possible that a single lysine tracts interacts with a single partner simultaneously (meaning the tract contributes a valence of 1) I don't think the authors can know that, so it may be wise to avoid specifying the specific valence.

Thank you for pointing this out. We agree with the reviewer's interpretation and have removed our initial interpretation from the text and simply state that a copy number of at least two is required for RPA43’s integration into the nucleolus.

The authors make reference to Q/H LCRs. Recent work from Gutiérrez et al. eLife (2022) has argued that histidine-richness in some glutamine-rich LCRs is above the number expected based on codon bias, and may reflect a mode of pH sensing. This may be worth discussing.

We appreciate the reviewer pointing out this publication. While this manuscript wasn’t published when we wrote our paper, upon reading it we agree it has some very relevant findings. We have added a reference to this manuscript in our discussion when discussing Q/H-rich LCRs.

Eric Ross has a number of very nice papers on this topic, but sadly I don't think any of them are cited here. On the question of LCR composition and condensate recruitment, I would recommend Boncella et al. PNAS (2020). On the question of proteome-wide LCR analysis, see Cascarina et al PLoS CompBio (2018) and Cascarina et al PLoS CompBio 2020.

We appreciate the reviewer for noting this related body of work. We have updated the citations to include work from Eric Ross where relevant.

Author Response

Reviewer #1 (Public Review):

This study examines the factors underlying the assembly of MreB, an actin family member involved in mediating longitudinal cell wall synthesis in rod-shaped bacteria. Required for maintaining rod shape and essential for growth in model bacteria, single molecule work indicates that MreB forms treadmilling polymers that guide the synthesis of new peptidoglycan along the longitudinal cell wall. MreB has proven difficult to work with and the field is littered with artifacts. In vitro analysis of MreB assembly dynamics has not fared much better as helpfully detailed in the introduction to this study. In contrast to its distant relative actin, MreB is difficult to purify and requires very specific conditions to polymerize that differ between groups of bacteria. Currently, in vitro analysis of MreB and related proteins has been mostly limited to MreBs from Gram-negative bacteria which have different properties and behaviors from related proteins in Gram-positive organisms.

Here, Mao and colleagues use a range of techniques to purify MreB from the Gram-positive organism Geobacillus stearothermophilus, identify factors required for its assembly, and analyze the structure of MreB polymers. Notably, they identify two short hydrophobic sequences-located near one another on the 3-D structure-which are required to mediate membrane anchoring.

With regard to assembly dynamics, the authors find that Geobacillus MreB assembly requires both interactions with membrane lipids and nucleotide binding. Nucleotide hydrolysis is required for interaction with the membrane and interaction with lipids triggers polymerization. These experiments appear to be conducted in a rigorous manner, although the salt concentration of the buffer (500mM KCl) is quite high relative to that used for in vitro analysis of MreBs from other organisms. The authors should elaborate on their decision to use such a high salt buffer, and ideally, provide insight into how it might impact their findings relative to previous work.

Response 1.1. MreB proteins are notoriously difficult to maintain in a soluble form. Some labs deleted the N-terminal amphipathic or hydrophobic sequences to increase solubility, while other labs used full-length protein but high KCl concentration (300 mM KCl) (Harne et al, 2020; Pande et al., 2022; Popp et al, 2010; Szatmari et al, 2020). Early in the project, we tested many conditions and noticed that high KCl helped keeping a slightly better solubility of full length MreBGs, without the need for deleting a part of the protein. In addition, concentrations of salt > 100 mM would better mimic the conditions met by the protein in vivo. While 50-100 mM KCl is traditionally used in actin polymerization assays, physiological salt concentrations are around 100-150 mM KCl in invertebrates and vertebrates (Schmidt-Nielsen, 1975), around 50-250 in fungal and plant cells (Rodriguez-Navarro, 2000) and 200-300 mM in the budding yeast (Arino et al, 2010). However, cytoplasmic K+ concentration varies greatly (up to 800 mM) depending on the osmolality of the medium in both E. coli (Cayley et al, 1991; Epstein & Schultz, 1965; Rhoads et al, 1976), and B. subtilis, in which the basal intracellular concentration of KCl was estimated to be ~ 350 mM (Eisenstadt, 1972; Whatmore et al, 1990). 500 mM KCl can therefore be considered as physiological as 100 mM KCl for bacterial cells. Since we observed plenty of pairs of protofilaments at 500 mM KCl and this condition helped to avoid aggregation, we kept this high concentration as a standard for most of our experiments. Nonetheless, we had also performed TEM polymerization assays at 100 mM in line with most of MreB and F-actin in vitro literature, and found no difference in the polymerization (or absence of polymerization) conditions. This was indicated in the initial submission (e.g. M&M section L540 and footnote of Table S2) but since two reviewers bring it up as a main point, it is evident we failed at communicating it clearly, for which we apologize. This has been clarified in the revised version of the manuscript. We have also almost systematically added the 100 mM KCl concentration too as per reviewer #2 request and to conciliate our salt conditions with those used for some in vitro analysis of MreBs from other organisms (see also response to reviewer #2 comments 1A and 1B = Responses 2.1A, 2.1B below). We then decided to refer to the 100 mM KCl concentration as our “standard condition” in the revised version of the manuscript, but we compile and compare the results obtained at 500 mM too, as both concentrations are within the physiological range in Bacillus.

Additionally, this study, like many others on MreB, makes much of MreB's relationship to actin. This leads to confusion and the use of unhelpful comparisons. For example, MreB filaments are not actin-like (line 58) any more than any polymer is "actin-like." As evidenced by the very beautiful images in this manuscript, MreB forms straight protofilaments that assemble into parallel arrays, not the paired-twisted polymers that are characteristic of F-actin. Generally, I would argue that work on MreB has been hindered by rather than benefitted from its relationship to actin (E.g early FP fusion data interpreted as evidence for an MreB endoskeleton supporting cell shape or depletion experiments implicating MreB in chromosome segregation) and thus such comparisons should be avoided unless absolutely necessary.

Response 1.2. We completely agree with reviewer #1 regarding unhelpful comparisons of actin and MreB, and that work on MreB has been traditionally hindered from its relationship to eukaryotic actin. MreB is nonetheless a structural homolog of actin, with a close structural fold and common properties (polymerization into pairs of protofilaments, ATPase activity…). It still makes sense to refer to a protein with common features, common ancestry and widely studied as long as we don’t enclose our mind into a conceptual framework. This said, actin and MreB diverged very early in evolution, which may account for differences in their biochemical properties and cellular functions. Current data on MreB filaments confirm that they display F-actin-like and F-actin-unlike properties. We thank the reviewer for this insightful comment. We have revised the text to remove any inaccurate or unhelpful comparison to actin (in particular the ‘actin-like filaments’ statement, previously used once)

Reviewer #2 (Public Review):

The paper "Polymerization cycle of actin homolog MreB from a Gram-positive bacterium" by Mao et al. provides the second biochemical study of a gram-positive MreB, but importantly, the first study examines how gram-positive MreB filaments bind to membranes. They also show the first crystal structure of a MreB from a Gram-positive bacterium - in two nucleotide-bound forms, finally solving structures that have been missing for too long. They also elucidate what residues in Geobacillus MreB are required for membrane associations. Also, the QCM-D approach to monitoring MreB membrane associations is a direct and elegant assay.

While the above findings are novel and important, this paper also makes a series of conclusions that run counter to multiple in vitro studies of MreBs from different organisms and other polymers with the actin fold. Overall, they propose that Geobacillus MreB contains biochemical properties that are quite different than not only the other MreBs examined so far but also eukaryotic actin and every actin homolog that has been characterized in vitro. As the conclusions proposed here would place the biochemical properties of Geobacillus MreB as the sole exception to all other actin fold polymers, further supporting experiments are needed to bolster these contrasting conclusions and their overall model.

Response 2.0. We are grateful to reviewer #2 for stressing out the novelty and importance of our results. Most of our conclusions were in line with previous in vitro studies of MreBs (formation of pairs of straight filaments on a lipid layer, both ATP and GTP binding and hydrolysis, distortion of liposomes…), to the exception of the claimed requirement of NTP hydrolysis for membrane binding prior to polymerization based on the absence of pairs of filaments in free solution or in the presence of AMP-PNP in our experimental conditions (which we agree was not sufficient to make such a bold claim, see below). Thanks to the reviewer’s comments, we have performed many controls and additional experiments that lead us to refine our results and largely conciliate them with the literature. Please see the answer to the global review comments - our conclusions have been revised on the basis of our new data.

1. (Difference 1) - The predominant concern about the in vitro studies that makes it difficult to evaluate many of their results (much less compare them to other MreB/s and actin homologs) is the use of a highly unconventional polymerization buffer containing 500(!) mM KCL. As has been demonstrated with actin and other polymers, the high KCl concentration used here (500mM) is certain to affect the polymerization equilibria, as increasing salt increases the hydrophobic effect and inhibits salt bridges, and therefore will affect the affinity between monomers and filaments. For example, past work has shown that high salt greatly changes actin polymerization, causing: a decreased critical concentration, increased bundling, and a greatly increased filament stiffness (Kang et al., 2013, 2012). Similarly, with AlfA, increased salt concentrations have been shown to increase the critical concentration, decrease the polymerization kinetics, and inhibit the bundling of AlfA filaments (Polka et al., 2009).

A more closely related example comes from the previous observation that increasing salt concentrations increasingly slow the polymerization kinetics of B. subtilis MreB (Mayer and Amann, 2009). Lastly, These high salt concentrations might also change the interactions of MreB(Gs) with the membrane by screening charges and/or increasing the hydrophobic effect. Given that 500mM KCl was used throughout this paper, many (if not all) of the key experiments should be repeated in more standard salt concentration (~100mM), similar to those used in most previous in vitro studies of polymers.

Response 2.1A. As per reviewer #2 request, we have done at 100 mM KCl too most experiments (TEM, cryo-EM, QCMD and ATPase assays) initially performed at 500 mM KCl only. The KCl concentration affects both membrane binding and filament stiffness as anticipated by the reviewer but the main conclusions are the same. The revised version of the manuscript compiles and compares the results obtained at both high and low [KCl], both concentrations being within the physiological range in Bacillus. Please see point 1 of the response to the global review comments and the first response to reviewer 1 (Response 1.1) for further elaboration.

Please note that in Mayer & Amann, 2009 (B. subtilis MreB), light scattering in free solution was inversely proportional to the KCl concentration, with the higher light scattering signal at 0 mM KCl (!), a > 2-fold reduction below 30 mM KCl and no scatter at all at 250 mM, suggesting a “salting in” phenomenon (see also the “Other Points to address” answers 1A and 2, below) (Mayer & Amann, 2009). Since no effective polymer formation (e.g. polymers shown by EM) was demonstrated in these experiments, it cannot be excluded that KCl was simply preventing aggregation of B. subtilis MreB in solution, as we observe. For all their other light scattering experiments, the ‘standard polymerization condition’ used by Mayer & Amann was 0.2 mM ATP, 5 mM MgCl2, 1 mM EGTA and 10 mM imidazole pH 7.0, to which MreB (in 5 mM Tris pH 8.0) was added. No KCl was present in their ‘standard’ polymerization conditions.

This would test if the many divergent properties of MreB(Gs) reported here arise from some difference in MreB(Gs) relative to other MreBs (and actin homologs), or if they arise from the 400mM difference in salt concentration between the studies. Critically, it would also allow direct comparisons to be made relative to previous studies of MreB (and other actin homologs) that used much lower salt, thereby allowing them to definitively demonstrate whether MreB(Gs) is indeed an outlier relative to other MreB and actin homologs. I would suggest using 100mM KCL, as historically, all polymerization assays of actin and numerous actin homologs have used 50-100mM KCL: 50mM KCl (for actin in F buffer) or 100mM KCl for multiple prokaryotic actin homologs and MreB (Deng et al., 2016; Ent et al., 2014; Esue et al., 2006, 2005; Garner et al., 2004 ; Polka et al., 2009 ; Rivera et al., 2011 ; Salje et al., 2011). Likewise, similar salt concentrations are standard for tubulin (80 mM K-Pipes) and FtsZ (100 mM KCl or 100mM KAc in HMK100 buffer).

Response 2.1B. We appreciate the reviewer’s feedback on this point. Please note that, although actin polymerization assays are historically performed at 50-100 mM KCl and thus 100 mM KCl was used for other bacterial actin homologs (MamK, ParM and AlfA), MreB polymerization assays have previously been reported at 300 mM KCl too (Harne et al., 2020; Pande et al., 2022; Popp et al., 2010; Szatmari et al., 2020), which is closer to the physiological salt concentration in bacterial cells (see Response 1.1), but also in the absence of KCl (see above). As a matter of fact, we originally wanted to use a “standard polymerization condition” based on the literature on MreB, before realizing there was none: only half used KCl (the other half used NaCl, or no monovalent salt at all) and among these, KCl concentrations varied (out of 8 publications, 2 used 20 mM KCl, 2 used 50 mM KCl and 4 used 300 mM KCl).

1. (Difference 2) - One of the most important differences claimed in this paper is that MreB(Gs) filaments are straight, a result that runs counter to the curved T. Maritima and C. crescentus filaments detailed by the Löwe group (Ent et al., 2014; Salje et al., 2011). Importantly, this difference could also arise from the difference in salt concentrations used in each study (500mM here vs. 100mM in the Löwe studies), and thus one cannot currently draw any direct comparisons between the two studies.

One example of how high salt could be causing differences in filament geometry: high salts are known to greatly increase the bending stiffness of actin filaments, making them more rigid (Kang et al., 2013). Likewise, increasing salt is known to change the rigidity of membranes. As the ability of filaments to A) bend the membrane or B) Deform to the membrane depends on the stiffness of filaments relative to the stiffness of the membrane, the observed difference in the "straight vs. curved" conformation of MreB filaments might simply arise from different salt concentrations. Thus, in order to draw several direct comparisons between their findings and those of other MreB orthologs (as done here), the studies of MreB(GS) confirmations on lipids should be repeated at the same buffer conditions as used in the Löwe papers, then allowing them to be directly compared.

Response 2.2. We fully agreed with reviewer #2 that the salts could be affecting the assay and did cryo-EM experiments also in the presence of 100 mM KCl as requested. The results unambiguously showed countless curved liposomes on the contact areas with MreB (Fig. 2F-G and Fig. 2-S5), very similar to what was reported for Thermotoga and Caulobacter MreBs by the Lowe group. Our results therefore confirm the previous findings that MreBs can bend lipids, and suggest that, indeed, high salt may increase filament stiffness as it has been shown for actin filaments. We are very grateful to reviewer #2 for his suggestion and for drawing our attention to the work of Kang et al, 2013. The different bending observed when varying the salt concentration raise relevant questions regarding the in vivo behavior of MreB, since KCl was shown to vary greatly depending on the medium composition. The manuscript has been updated accordingly in the Results (from L243) and Discussion sections (L585-595).

1. (Difference 3) - The next important difference between MreB(Gs) and other MreBs is the claim that MreB polymers do not form in the absence of membranes.

A) This is surprising relative to other MreBs, as MreBs from 1) T. maritime (multiple studies), E.coli (Nurse and Marians, 2013), and C. crescentus (Ent et al., 2014) have been shown to form polymers in solution (without lipids) with electron microscopy, light scattering, and time-resolved multi-angle light scattering. Notably, the Esue work was able to observe the first phase of polymer formation and a subsequent phase of polymer bundling (Esue et al., 2006) of MreB in solution. 2) Similarly, (Mayer and Amann, 2009) demonstrated B. subtilis MreB forms polymers in the absence of membranes using light scattering.

Response 2.3A. The literature does convincingly show that Thermotoga MreB forms polymers in solution, without lipids (note that for Caulobacter MreB filaments were only reported in the presence of lipids, (van den Ent et al, 2014)). Assemblies reported in solution are bundles or sheets (included in at the earlier time points in the time-resolved EM experiments reported by Esue et al. 2006 mentioned by the reviewer – ‘2 minutes after adding ATP, EM revealed that MreB formed short filamentous bundles’) (Esue et al, 2006). However, and as discussed above (Response 2.1A), the light scattering experiments in Mayer et Amann, 2009 do not conclusively demonstrate the presence of polymers of B. subtilis MreB in solution (Mayer & Amann, 2009). We performed many light scattering experiments of B. subtilis MreB in solution in the past (before finding out that filaments were only forming in the presence of lipids), and got similar scattering curves (see two examples of DLS experiments in Author response image 1) in conditions in which NO polymers could ever been observed by EM while plenty of aggregates were present.

Author response image 1.

We did not consider these results publishable in the absence of true polymers observed by TEM. As pointed out on the interesting study from Nurse et al. (on E. coli MreB) (Nurse & Marians, 2013), one cannot rely only on light scattering only because non-specific aggregates would show similar patterns than polymers. Over the last two decades, about 15 publications showed polymers of MreB from several Gram-negative species, while none (despite the efforts of many) showed a single convincing MreB polymer from a Gram-positive bacterium by EM. A simple hypothesis is that a critical parameter was missing, and we present convincing evidence that lipids are critical for Geobacillus MreB to form pairs of filaments in the conditions tested. However, in solution too we do occasionally see pairs of filaments (Fig 2-S2), and also sheet-like structures among aggregates when the concentration of MreB is increased (Fig. 2-S2 and Fig. 3-S2). Thus, we agree with the reviewer that it cannot be claimed that Geobacillus MreB is unable to polymerize in the absence of lipids, but rather that lipids strongly stimulate its polymerization, condition depending.

B) The results shown in figure 5A also go against this conclusion, as there is only a 2-fold increase in the phosphate release from MreB(Gs) in the presence of membranes relative to the absence of membranes. Thus, if their model is correct, and MreB(Gs) polymers form only on membranes, this would require the unpolymerized MreB monomers to hydrolyze ATP at 1/2 the rate of MreB in filaments. This high relative rate of hydrolysis of monomers compared to filaments is unprecedented. For all polymers examined so far, the rate of monomer hydrolysis is several orders of magnitude less than that of the filament. For example, actin monomers are known to hydrolyze ATP 430,000X slower than the monomers inside filaments (Blanchoin and Pollard, 2002; Rould et al., 2006).

Response 2.3B. We agree with the reviewer. We have now found conditions where sheets of MreB form in solution (at high MreB concentration) in the presence of ADP and AMP-PNP. However, we have now added several controls that exclude efficient formation of polymers in solution in the presence of ATP at low concentrations of MreBGs (≤ 1.5 µM), the condition used for the malachite green assays. At these MreB concentrations, pairs of filaments are observed in the presence of lipids, but very unfrequently in solution, and sheets are not observed in solution either (Fig. 2-S2A, B). Yet, albeit puzzling, in these conditions Pi release is reproducibly observed in solution, reduced only ~ 2 to 3-fold relative to Pi release in the presence of lipids (Fig. 5A and Fig. 5-S1). A reinforcing observation is when the ATPase assays is performed at 100 mM KCl (Fig. 5A). In this condition MreB binding to lipids is increased relative to 500 mM KCl (Fig. 4-S4C), and the stimulation of the ATPase activity by the presence of lipids is also stronger that at 500 mM (Fig. 5-S1A). Further work is needed to characterize in detail the ATPase activity of MreB proteins, for which data in the literature is very scarce. We can’t exclude that MreB could nucleate in solution or form very unstable filaments that cannot be seen in our EM assay but consume ATP in the process. At the moment, the significance of the Pi released in solution is unknown and will require further investigation.

C) Thus, there is a strong possibility that MreB(Gs) polymers are indeed forming in solution in addition to those on the membrane, and these "solution polymers" may not be captured by their electron microscopy assay. For example, high salt could be interfering with the absorption of filaments to glow discharged lacking lipids.

Response 2.3C. We appreciate the reviewer’s insight about this critical point. Polymers presented in the original Fig. 2A were obtained at 500 mM KCl but we had tested the polymerization of MreB at 100 mM KCl as well, without noticing differences. We have nonetheless redone this quantitatively and used these data for the revised Fig. 2A, as we are now using 100 mM KCl as our standard polymerization condition throughout the revised manuscript. We also followed the other suggestion of the reviewer and tested glow discharged grids (a more classic preparation for soluble proteins) vs non-glow discharged EM grids, as well as a higher concentration of MreB. Grids are generally glow-discharged to make them hydrophilic in order to adsorb soluble proteins, but the properties of MreB (soluble but obviously presenting hydrophobic domains) made difficult to predict what support putative soluble polymers would preferentially interact with. Septins for example bind much better to hydrophobic grids despite their soluble properties (I. Adriaans, personal communication). Virtually no double filaments were observed in solution at either low or high [MreB]. The fact that in some conditions (high [MreB], other nucleotides) we were able to detect sheet-like structures excluded a technical issue that would prevent the detection of existing but “invisible” polymers here. We have added these new data in Fig. 2-S2.

As indicated above, the reviewer’s comments made us realize that we could not state or imply that MreB cannot polymerize in the absence of lipids. As a matter of fact, we always saw some random filaments in the EM fields, both in solution and in the presence of non-hydrolysable analogues, at very low frequency (Fig. 2A). And we do see now sheets at high MreB concentration (Fig. 2-S2B). We could be just missing the optimal conditions for polymerisation in solution, while our phrasing gave the impression that no polymers could ever form in the absence of ATP or lipids. Therefore, we have:

1) analyzed all TEM data to present it as semi-quantitative TEM, using our methodology originally implemented for the analysis of the mutants

2) reworked the text to remove any issuing statements and to indicate that MreBGs was only found to bind to a lipid monolayer as a double protofilament in the presence of ATP/GTP but that this does not exclude that filaments may also form in other conditions.

In order to definitively prove that MreB(Gs) does not have polymers in solution, the authors should:

i) conduct orthogonal experiments to test for polymers in solution. The simplest test of polymerization might be conducting pelleting assays of MreB(Gs) with and without lipids, sweeping through the concentration range as done in 2B and 5a.

Response 2.3Ci. Following reviewer #2 suggestion, we conducted a series of sedimentation assays in the presence and in the absence of lipids, at low (100 mM) and high (500 mM) salt, for both the wild-type protein and the three membrane-anchoring mutants (all at 1.3 µM). Sedimentation experiments in salt conditions preventing aggregation in solution (500 mM KCl) fitted with our TEM results: MreB wild-type pelleting increased in the presence of both ATP and lipids (Fig. R1). The sedimentation was further increased at 100 mM KCl, which would fit our other results indicating an increased interaction of MreB with the membrane. However, in addition to be poorly reproducible (in our hands), the approach does not discriminate between polymers and aggregates (or monomers bound to liposomes) and since MreB has a strong tendency to aggregate, we believe that the technique is ill-suited to reliably address MreB polymerization and prefer not to include sedimentation data in our manuscript. The recent work from Pande et al. (2022) illustrates well this issue since no sedimentation of MreB (at 2 µM) was observed in solution in conditions supporting polymerization (at 300 mM KCl): ‘the protein does not pellet on its own in the absence of liposome, irrespective of its polymerization state’, implying that sedimentation does not allow to detect MreB5 filaments in solution (Pande et al., 2022).

ii) They also could examine if they see MreB filaments in the absence of lipids at 100mM salt (as was seen in both Löwe studies), as the high salt used here might block the charges on glow discharged grids, making it difficult for the polymer to adhere.

See above, Response 2.3C

iii) Likewise, the claim that MreB lacking the amino-terminus and the α2β7 hydrophobic loop "is required for polymerization" is questionable as if deleting these resides blocks membrane binding, the lack of polymers on the membrane on the grid is not unexpected, as these filaments that cannot bind the membrane would not be observable. Given these mutants cannot bind the membrane, mutant polymers could still indeed exist in solution, and thus pelleting assays should be used to test if non-membrane associated filaments composed of these mutants do or do not exist.

Response 2.3Ciii. This is a fair point, we thank the reviewer for this remark. We did not mean to state or imply that the hydrophobic loop was required for polymerization per se, but that polymerization into double filaments only efficiently occurs upon membrane binding, which is mediated by the two hydrophobic sequences. We tested all three mutants by sedimentation as suggested by reviewer #2. In the salt condition that limits aggregation (500 mM KCl) the mutants did not pellet while the wild-type protein did (in the presence of lipids) (Fig. R2 below), in agreement with our EM data. We tested the absence of lipids on the mutant bearing the 2 deletions and observed that the (partial) sedimentation observed at low KCl concentration was ATP and lipid dependent (Fig. R3).

Given our concerns about MreB sedimentation assays (see above, Response 2.3Ci), we prefer not to include these sedimentation data in our manuscript. Instead, we tested by TEM the possible polymerization of the mutants in solution (we only tested them in the presence of lipids in the initial submission). No filaments were detected in solution for any of the mutants (Fig. 4-S3A).

A final note, the results shown in "Figure 1 - figure supplement 2, panel C" appear to directly refute the claim that MreB(Gs) requires lipids to polymerize. As currently written, it appears they can observe MreB(Gs) filaments on EM grids without lipids. If these experiments were done in the presence of lipids, the figure legend should be updated to indicate that. If these experiments were done in the absence of lipids, the claim that membrane association is required for MreB polymerizations should be revised.

The TEM experiments show were indeed performed in the presence of lipids. We apologize for this was not clearly stated in the legend. To prevent all confusion, we have nevertheless removed these images in this figure since the polymerization conditions and lipid requirement are not yet presented when this figure is referred to in the text. We have instead added a panel with the calibration curve for the size exclusion profiles as per request of reviewer #3. The main point of this figure is to show the tendency of MreBGs to aggregate: analytical size-exclusion chromatography shows a single peak corresponding to the monomeric MreBGs, molecular weight ~ 37 KDa, in our purification conditions, but it can readily shift to a peak corresponding to high MW aggregates, depending on the protein concentration and/or storage conditions.

1. (Difference 4) - The next difference between this study and previous studies of MreB and actin homologs is the conclusion that MreB(Gs) must hydrolyze ATP in order to polymerize. This conclusion is surprising, given the fact that both T. Maritima (Salje · 2011, Bean 2008) and B. subtilis MreB (Mayer 2009) have been shown to polymerize in the presence of ATP as well as AMP-PNP.

Likewise, MreB polymerization has been shown to lag ATP hydrolysis in not only T. maritima MreB (Esue 2005), eukaryotic actin, and all other prokaryotic actin homologs whose polymerization and phosphate release have been directly compared: MamK (Deng et al., 2016), AlfA (Polka et al., 2009), and two divergent ParM homologs (Garner et al., 2004; Rivera et al., 2011). Currently, the only piece of evidence supporting the idea that MreB(Gs) must hydrolyze ATP in order to polymerize comes from 2 observations: 1) using electron microscopy, they cannot see filaments of MreB(Gs) on membranes in the presence of AMP-PNP or ApCpp, and 2) no appreciable signal increase appears testing AMPPNP- MreB(Gs) using QCM-D. This evidence is by no means conclusive enough to support this bold claim: While their competition experiment does indicate AMPPNP binds to MreB(Gs), it is possible that MreB(Gs) cannot polymerize when bound to AMPPNP.

For example, it has been shown that different actin homologs respond differently to different non-hydrolysable analogs: Some, like actin, can hydrolyze one ATP analog but not the other, while others are able to bind to many different ATP analogs but only polymerize with some of one of them.

Response 2.4. We agree with the reviewer, it is uncertain what analogs bind because they are quite different to ATP and some proteins just do not like them, they can change conditions such that filaments stop forming as well and be (theoretically) misleading. This is why we had tested ApCpp in addition to AMP-PNP as non-hydrolysable analog (Fig. 3A). As indicated above, our new complementary experiments (Fig. 3-S1B-D) now show that some rare (i.e. unfrequently and in limited amount) dual polymers are detected in the presence of ApCpp (Fig. 3A) and at high MreB concentration only in the presence of AMP-PNP (Fig. 3-S1B-D), suggesting different critical concentrations in the presence of alternative nucleotides. We have dampened our conclusions, in the light of our new data, and modified the discussion accordingly.

Thus, to further verify their "hydrolysis is needed for polymerization" conclusion, they should:

A. Test if a hydrolysis deficient MreB(Gs) mutant (such as D158A) is also unable to polymerize by EM.

Response 2.4A. We thank the reviewer for this suggestion. As this conclusion has been reviewed on the basis of our new data (see previous response), testing putative ATPase deficient mutants is no longer required here. The study of ATPase mutants is planned for future studies (see Response 3.10 to reviewer #3).

B. They also should conduct an orthogonal assay of MreB polymerization aside from EM (pelleting assays might be the easiest). They should test if polymers of ATP, AMP-PNP, and MreB(Gs)(D158A) form in solution (without membranes) by conducting pelleting assays. These could also be conducted with and without lipids, thereby also addressing the points noted above in point 3.

Response 2.4B. Please see Response 2.3Ci above.

C. Polymers may indeed form with ATP-gamma-S, and this non-hydrolysable ATP analog should be tested.

Response 2.4C. It is fairly possible that ATP-γ-S supports polymerization since it is known to be partially hydrolysable by actin giving a mild phenotype (Mannherz et al, 1975). This molecule can even be a bona fide substrate for some ATPases (e.g. (Peck & Herschlag, 2003). Thus, we decided to exclude this “non-hydrolysable” analog and tested instead AMP-PNP and ApCpp. We know that ATP-γ-S has been and it is still frequently used, but we preferred to avoid it for the moment for the above-indicated reasons. We chose AMPPNP and AMPPCP instead because (1) they were shown to be completely non-hydrolysable by actin, in contrast to ATP-γ-S; (2) they are widely used (the most commonly used for structural studies; (Lacabanne et al, 2020), (3) AMPPNP was previously used in several publications on MreB (Bean & Amann, 2008; Nurse & Marians, 2013; Pande et al., 2022; Popp et al., 2010; Salje et al, 2011; van den Ent et al., 2014)and thus would allow direct comparison. AMPPCP was added to confirm the finding with AMP-PNP. There are many other analogs that we are planning to explore in future studies (see next Response, 2.4D).

D. They could also test how the ADP-Phosphate bound MreB(Gs) polymerizes in bulk and on membranes, using beryllium phosphate to trap MreB in the ADP-Pi state. This might allow them to further refine their model.

Response 2.4D. We plan to address the question of the transition state in depth in following-up work, using a series of analogs and mutants presumably affected in ATPase activity, both predicted and identified in a genetic screen. As indicated above, it is uncertain what analogs bind because they are quite different to ATP and some may bind but prevent filament formation. Thus, we anticipate that trying just one may not be sufficient, they can change conditions and be (theoretically) misleading and thus a thorough analysis is needed to address this question. Since our model and conclusions have been revised on the basis of our new data, we believe that these experiments are beyond the scope of the current manuscript.

E. Importantly, the Mayer study of B. subtilis MreB found the same results in regard to nucleotides, "In polymerization buffer, MreB produced phosphate in the presence of ATP and GTP, but not in ADP, AMP, GDP or AMP-PNP, or without the readdition of any nucleotide". Thus this paper should be referenced and discussed

Response 2.4E. We agree that Pi release was detected previously. We have added the reference (L121)

1. (Difference 5) - The introduction states (lines 128-130) "However, the need for nucleotide binding and hydrolysis in polymerization remains unclear due to conflicting results, in vivo and in vitro, including the ability of MreB to polymerize or not in the presence of ADP or the non-hydrolysable ATP analog AMP-PNP."

A) While this is a great way to introduce the problem, the statement is a bit vague and should be clarified, detaining the conflicting results and appropriate references. For example, what conflicting in vivo results are they referring to? Regarding "MreB polymerization in AMP-PNP", multiple groups have shown the polymerization of MreB(Tm) in the presence of AMP-PNP, but it is not clear what papers found opposing results.

Response 2.5A. Thanks for the comment. We originally did not detail these ‘conflicting results’ in the Introduction because we were doing it later in the text, with the appropriate references, in particular in the Discussion (former L433-442). We have now removed this from the Discussion section and added a sentence in the introduction too (L123-130) quickly detailing the discrepancies and giving the references.

• For more clarity, we have removed the “in vivo” (which referred to the distinct results reported for the presumed ATPase mutants by the Garner and Graumann groups) and focus on the in vitro discrepancies only.

• These discrepancies are the following: while some studies showed indeed polymerization (as assessed by EM) of MreBTm in the presence of AMPPNP, the studies from Popp et al and Esue et al on T. maritima MreB, and of Nurse et al on E. coli MreB reported aggregation in the presence of AMP-PNP (Esue et al., 2006; Popp et al., 2010) or ADP (Nurse & Marians, 2013), or no assembly in the presence of ADP (Esue et al., 2006). As for the studies reporting polymerization in the presence of AMP-PNP by light scattering only (Bean & Amann, 2008; Gaballah et al, 2011; Mayer & Amann, 2009; Nurse & Marians, 2013), they could not differentiate between aggregates or true polymers and thus cannot be considered conclusive.

B) The statement "However, the need for nucleotide binding and hydrolysis in polymerization remains unclear due to conflicting results, in vivo and in vitro, including the ability of MreB to polymerize or not in the presence of ADP or the non-hydrolyzable ATP analog AMP-PNP" is technically incorrect and should be rephrased or further tested.

i. For all actin (or tubulin) family proteins, it is not that a given filament "cannot polymerize" in the presence of ADP but rather that the ADP-bound form has a higher critical concentration for polymer formation relative to the ATP-bound form. This means that the ADP polymers can indeed polymerize, but only when the total protein exceeds the ADP critical concentration. For example, many actin-family proteins do indeed polymerize in ADP: ADP actin has a 10-fold higher critical concentration than ATP actin, (Pollard, 1984) and the ADP critical concentrations of AlfA and ParM are 5X and 50X fold higher (respectively) than their ATP-bound forms(Garner et al., 2004; Polka et al., 2009)

Response 2.5Bi. Absolutely correct. We apologize for the lack of accuracy of our phrasing and have corrected it (L123).

ii. Likewise, (Mayer and Amann, 2009) have already demonstrated that B. subtilis MreB can polymerize in the presence of ADP, with a slightly higher critical concentration relative to the ATP-bound form.

Response 2.5Bii. In Mayer and Amann, 2009, the same light scattering signal (interpreted as polymerization) occurred regardless of the nucleotide, and also in the absence of nucleotide (their Fig. 10) and ATP-, ADP- and AMP-PNP-MreB ‘displayed nearly indistinguishable critical concentrations’. They concluded that MreB polymerization is nucleotide-independent. Please see below (responses to ’Other points to address’) our extensive answer to the Mayer & Amann recurring point of reviewer #2

Thus, to prove that MreB(Gs) polymers do not form in the presence of ADP would require one to test a large concentration range of ADP-bound MreB(Gs). They should test if ADP- MreB(Gs) polymerizes at the highest MreB(Gs) concentrations that can be assayed. Even if this fails, it may be the MreB(Gs) ADP polymerizes at higher concentrations than is possible with their protein preps (13uM). An even more simple fix would be to simply state MreB(Gs)-ADP filaments do not form beneath a given MreB(Gs) concentration.

We agree with the reviewer. Our wording was overstating our conclusions. Based on our new quantifications (Fig. 3-S1B, D), we have rephrased the results section and now indicate that pairs of filaments are occasionally observed in the presence of ADP in our conditions across the range of MreB concentration that could be tested, suggesting a higher critical concentration for MreB-ADP (L310-312). Only at the highest MreB concentration, sheet- and ribbon-like structures were observed in the presence of ADP (Fig. 3-S2B).

Other Points to address:

1) There are several points in this paper where the work by Mayer and Amann is ignored, not cited, or readily dismissed as "hampered by aggregation" without any explanation or supporting evidence of that fact.

We have cited the Mayer study where appropriate. However, we cannot cite it as proof of polymerization in such or such condition since their approach does not show that polymers were obtained in their conditions. Again, they based all their conclusions solely on light scattering experiments, which cannot differentiate between polymers and aggregates.

A) Lines 100-101 - While the irregular 3-D formations seen formed by MreB in the Dersch 2020 paper could be interpreted as aggregates, stating that the results from specifically the Gaballah and Meyer papers (and not others) were "hampered by aggregation" is currently an arbitrary statement, with no evidence or backing provided. Overall, these lines (and others in the paper) dismiss these two works without giving any evidence to that point. Thus, they should provide evidence for why they believe all these papers are aggregation, or remove these (and other) dismissive statements.

We apologize if our statements about these reports seemed dismissive or disrespectful, it was definitely not our intention. Light scattering shows an increase of size of particles over time, but there is no way to tell if the scattering is due to organized (polymers) or disorganized (aggregation) assemblies. Thus, it cannot be considered a conclusive evidence of polymerization without the proof that true filaments are formed by the protein in the conditions tested, as confirmed by EM for example. MreB is known to easily aggregate (see our size exclusion chromatography profiles and ones from Dersch 2020 (Dersch et al, 2020), and note that no chromatography profiles were shown in the Mayer report) and, as indicated above, we had similar light scattering results for MreB for years, while only aggregates could be observed by TEM (see above Response 2.3A). Several observations also suggest that aggregation instead of polymerization might be at play in the Mayer study, for example ‘polymerization’ occurring in salt-less buffer but ‘inhibited’ with as low as 100 mM KCl, which should rather be “salting in” (see below). We did not intend to be dismissive, but it seemed wrong to report their conclusions as conclusive evidence. We thought that we had cited these papers where appropriate but then explained that they show no conclusive proof of polymerization and why, but it is evident that we failed at communicating it clearly. We have reworked the text to remove any issuing and arbitrary statement about our concerns regarding these reports (e.g. L93 & L126).

One important note - There are 2 points indicating that dismissing the Meyer and Amann work as aggregation is incorrect:

1) the Meyer work on B. subtilis MreB shows both an ATP and a slightly higher ADP critical concentration. As the emergence of a critical concentration is a steady-state phenomenon arising from the association/dissociation of monomers (and a kinetically limiting nucleation barrier), an emergent critical concentration cannot arise from protein aggregation, critical concentrations only arise from a dynamic equilibrium between monomer and polymer.

• Critical concentration for ATP, ADP or AMPPNP were described in Mayer & Amann (Mayer & Amann, 2009) as “nearly indistinguishable” (see Response 2.5Bii)
• Protein aggregation depends on the solution (pH and ions), protein concentration and temperature. And above a certain concentration, proteins can become instable, thus a critical concentration for aggregation can emerge.

2) Furthermore, Meyer observed that increased salt slowed and reduced B. subtilis MreB light scattering, the opposite of what one would expect if their "polymerization signal" was only protein aggregation, as higher salts should increase the rate of aggregation by increasing the hydrophobic effect.

It is true that at high salt concentration proteins can precipitate, a phenomenon described as “salting out”. However, it is also true that salts help to solubilize proteins (“salting in”), and that proteins tend to precipitate in the absence of salt. Considering that the starting point of the Mayer and Amann experiment (Mayer & Amann, 2009) is the absence of salt (where they observed the highest scattering) and that they gradually reduce this scattering by increasing KCl (the scattering is almost abolished below 100 mM only!) it is plausible that a salting-in phenomenon might be at play, due to increased solubility of MreB by salt. In any case, this cannot be taken as a proof that polymerization rather than aggregation occurred.

B) Lines 113-137 -The authors reference many different studies of MreB, including both MreB on membranes and MreB polymerized in solution (which formed bundles). However, they again neglect to mention or reference the findings of Meyer and Amann (Mayer and Amann, 2009), as it was dismissed as "aggregation". As B. subtilis is also a gram-positive organism, the Meyer results should be discussed.

We did cite the Mayer and Amann paper but, as explained above, we cannot cite this study as an example of proven polymerization. We avoided as much as possible to polemicize in the text and cited this paper when possible. Again, we have reworked the text to avoid any issuing or dismissive statement. Also, we forgot mentioned this study at L121 as an example of reported ATPase activity, and this has now been corrected.

2) Lines 387-391 state the rates of phosphate release relative to past MreB findings: "These rates of Pi release upon ATP hydrolysis (~ 1 Pi/MreB in 6 min at 53{degree sign}C) are comparable to those observed for MreBTm and MreB(Ec) in vitro". While the measurements of Pi release AND ATP hydrolysis have indeed been measured for actin, this statement does not apply to MreB and should be corrected: All MreB papers thus far have only measured Pi release alone, not ATP hydrolysis at the same time. Thus, it is inaccurate to state "rates of Pi release upon ATP hydrolysis" for any MreB study, as to accurately determine the rate of Pi release, one must measure: 1. The rate of polymer over time, 2) the rate of ATP hydrolysis, and 3) the rate of phosphate release. For MreB, no one has, so far, even measured the rates of ATP hydrolysis and phosphate release with the same sample.

We completely agree with the reviewer, we apologize if our formulation was inaccurate. We have corrected the sentence (L479). Thank you for pointing out this mistake.

3) The interpretation of the interactions between monomers in the MreB crystal should be more carefully stated to avoid confusion. While likely not their intention, the discussions of the crystal packing contacts of MreB can appear to assume that the monomer-monomer contacts they see in crystals represent the contacts within actual protofilaments. One cannot automatically assume the observations of monomer-monomer contacts within a crystal reflect those that arise in the actual filament (or protofilament).

We agree, we thank the reviewer for his comments. We have revamped the corresponding paragraph.

A) They state, "the apo form of MreBGs forms less stable protofilaments than its G- homologs ." Given filaments of the Apo form of MreB(GS) or b. subtilis have never been observed in solution, this statement is not accurate: while the contacts in the crystal may change with and without nucleotide, if the protein does not form polymers in solution in the apo state, then there are no "real" apo protofilaments, and any statements about their stability become moot. Thus this statement should be rephrased or appropriately qualified.

see above.

B) Another example: while they may see that in the apo MreB crystal, the loop of domain IB makes a single salt bridge with IIA and none with IIB. This contrasts with every actin, MreB, and actin homolog studied so far, where domain IB interacts with IIB. This might reflect the real contacts of MreB(Gs) in the solution, or it may be simply a crystal-packing artifact. Thus, the authors should be careful in their claims, making it clear to the reader that the contacts in the crystal may not necessarily be present in polymerized filaments.

Again, we agree with the reviewer, we cannot draw general conclusions about the interactions between monomers from the apo form. We have rephrased this paragraph.

4) lines 201-202 - "Polymers were only observed at a concentration of MreB above 0.55 μM (0.02 mg/mL)". Given this concentration dependence of filament formation, which appears the same throughout the paper, the authors could state that 0.55 μM is the critical concentration of MreB on membranes under their buffer conditions. Given the lack of critical concentration measurement in most of the MreB literature, this could be an important point to make in the field.

Following reviewer’s #2 suggestion, we have now estimated the critical concentration (Cc=0.4485 µM) and reported it in the text. (L218).

5) Both mg/ml and uM are used in the text and figures to refer to protein concentration. They should stick to one convention, preferably uM, as is standard in the polymer field.

Sorry for the confusion. We have homogenized to MreB concentrations to µM throughout the text and figures.

6) Lines 77-78 - (Teeffelen et al., 2011) should be referenced as well in regard to cell wall synthesis driving MreB motion.

This has been corrected, sorry for omitting this reference.

7) Line 90 - "Do they exhibit turnover (treadmill) like actin filaments?". This phrase should be modified, as turnover and treadmilling are two very different things. Turnover is the lifetime of monomers in filaments, while treadmilling entails monomer addition at one end and loss at the other. While treadmilling filaments cause turnover, there are also numerous examples of non-treadmilling filaments undergoing turnover: microtubules, intermediate filaments, and ParM. Likewise, an antiparallel filament cannot directionally treadmill, as there is no difference between the two filament ends to confer directional polarity.

This is absolutely true, we apologize for our mistake. The sentence has been corrected (L82).

8) Throughout the paper, the term aggregation is used occasionally to describe the polymerization shown in many previous MreB studies, almost all of which very clearly showed "bundled" filaments, very distinct entities from aggregates, as a bundle of polymers cannot form without the filaments first polymerizing on their own. Evidence to this point, polymerization has been shown to precede the bundling of MreB(Tm) by (Esue et al., 2005).

We agree with reviewer #2 about polymers preceding bundles and “sheets”. However, we respectfully disagree that we used the word aggregation “throughout the paper” to describe structures that clearly showed polymers or sheets of filaments. A search (Ctrl-F: “aggreg”) reveals only 6 matches, 3 describing our own observations (L152, 163/5, and 1023/28), one referring to (Salje et al., 2011) (L107) but citing her claim that they observed aggregation (due to the N-terminus), and the last two (L100, L440) refer (again) to the Gaballah/Mayer/Dersch publications to say that aggregation could not be excluded in these reports as discussed above (Dersch et al., 2020; Gaballah et al., 2011; Mayer & Amann, 2009).

9) lines 106-108 mention that "The N-terminal amphipathic helix of E. coli MreB (MreBEc) was found to be necessary for membrane binding. " This is not accurate, as Salje observed that one single helix could not cause MreB to mind to the membrane, but rather, multiple amphipathic helices were required for membrane association (Salje et al., 2011).

Salje et al showed that in vivo the deletion of the helix abolishes the association of MreB to the membrane. This publication also shows that in vitro, addition of the helix to GFP (not to MreB) prompts binding to lipid vesicles, and that this was increased if there are 2 copies of the helix, but they could not test this directly in vitro with MreB (which is insoluble when expressed with its N-terminus). This prompted them to speculate that multiple MreBs could bind better to the membrane than monomers. However, this remained to be demonstrated. Additional hydrophobic regions in MreB such as the hydrophobic loop could participate to membrane anchoring but are absent in their in vitro assays with GFP.

The Salje results imply that dimers (or further assemblies) of MreB drive membrane association, a point that should be discussed in regard to the question "What prompts the assembly of MreB on the inner leaflet of the cytoplasmic membrane?" posed on lines 86-87.

We agree that this is an interesting point. As it is consistent with our results, we have incorporated it to our model (Fig. 6) and we are addressing it in the discussion L573-575.

10) On lines 414-415, it is stated, "The requirement of the membrane for polymerization is consistent with the observation that MreB polymeric assemblies in vivo are membrane-associated only." While I agree with this hypothesis, it must be noted that the presence or absence of MreB polymers in the cytoplasm has not been directly tested, as short filaments in the cytoplasm would diffuse very quickly, requiring very short exposures (<5ms) to resolve them relative to their rate of diffusion. Thus, cytoplasmic polymers might still exist but have not been tested.

This is also an interesting point. Indeed if a nucleated form, or very short (unbundled) polymers exist in the cytoplasm, they have not been tested by fluorescence microscopy. However, the polymers that localize at the membrane (~ 200 nm), if soluble, would have been detected in the cytoplasm by the work of reviewer #2, us or others.

11) lines 429-431 state, "but polymerization in the presence of ADP was in most cases concluded from light scattering experiments alone, so the possibility that aggregation rather than ordered polymerization occurred in the process cannot be excluded."

A) If an increased light scattering signal is initiated by the addition of ADP (or any nucleotide), that signal must come from polymerization or multimerization. What the authors imply is that there must be some ADP-dependent "aggregation" of MreB, which has not been seen thus far for any polymer. Furthermore, why would the addition of ADP initiate aggregation?

We did not mean that ADP itself would prompt aggregation, but that the protein would aggregate in the buffer regardless of the presence of ADP or other nucleotides. The Mayer & Amann study claims that MreB “polymerization” is nucleotide-independent, as they got identical curves with ATP, ADP, AMPPNP and even with no nucleotides at all (Fig. 10 in their paper, pasted here) (Mayer & Amann, 2009).

Their experiments with KCl are also remarkable as when they lowered the salt they got faster and faster “polymerization”, with the strongest light scattering signal in the absence of any salt. The high KCl concentration in which they got almost no more “polymers” was 75 mM KCl, and ‘polymerization was almost entirely inhibited at 100 mM’ (Fig. 7, pasted below). Yet the intracellular level of KCl in bacteria is estimated to be ~300 mM (see Response 1.1)

B) Likewise, the statement "Differences in the purity of the nucleotide stocks used in these studies could also explain some of the discrepancies" is unexplained and confusing. How could an impurity in a nucleotide stock affect the past MreB results, and what is the precedent for this claim?

We meant that the presence of ATP in the ADP stocks might have affected the outcome of some assays, generating the conflicting results existing in the literature. We agree this sentence was confusing, we have removed it.

12) lines 467-469 state, "Thus, for both MreB and actin, despite hydrolyzing ATP before and after polymerization, respectively, the ADP-Pi-MreB intermediate would be the long-lived intermediate state within the filaments."

A) For MreB, this statement is extremely speculative and unbiased, as no one has measured 1) polymerization, 2) ATP hydrolysis, and 3) phosphate release. For example, it could be that ATP hydrolysis is slow, while phosphate release is fast, as is seen in the actin from Saccharomyces cerevisiae.

We agree that this was too speculative. This has been removed from the (extensively) modified Discussion section. Thanks for the comment.

B) For actin, the statement of hydrolysis of ATP of monomer occurring "before polymerization" is functionally irrelevant, as the rate of ATP hydrolysis of actin monomers is 430,000 times slower than that of actin monomers inside filaments (Blanchoin and Pollard, 2002; Rould et al., 2006).

We agree that the difference of hydrolysis rate between G-actin and F-actin implies that ATP hydrolysis occurs after polymerization. We are afraid that we do not follow the reviewer’s point here, we did not say or imply that ATP hydrolysis by actin monomers was functionally relevant.

13) Lines 442-444. "On the basis of our data and the existing literature, we propose that the requirement for ATP (or GTP) hydrolysis for polymerization may be conserved for most MreBs." Again, this statement both here (and in the prior text) is an extremely bold claim, one that runs contrary to a large amount of past work on not just MreB, but also eukaryotic actin and every actin homolog studied so far. They come to this model based on 1) one piece of suggestive data (the behavior of MreB(GS) bound to 2 non-hydrolysable ATP analogs in 500mM KCL), and 2) the dismissal (throughout the paper) of many peer-reviewed MreB papers that run counter to their model as "aggregation" or "contaminated ATP stocks ." If they want to make this bold claim that their finding invalidates the work of many labs, they must back it up with further validating experiments.

We respectfully disagree that our model was based on “one piece of suggestive data” and backed-up by dismissing most past work in the field. We only wanted to raise awareness about the conflicting data between some reports (listed in response 2.5a), and that the claims made by some publications are to be taken with caution because they only rely on light scattering or, when TEM was performed, showed only disorganized structures.

This said, we clearly failed in proposing our model and we are sorry to see that we really annoyed the reviewer with our suspicion that the work by Mayer & Amann reports aggregation. As indicated above, we have amended our manuscript relative to this point. We also agree that our suggestion to generalize our findings to most MreBs was unsupported, and overstated considering how confusing some result from the literature are. We have refined our model and reworked the text to take on board the reviewer’s remarks as well as the new data generated during the revision process.

We would like to thank reviewer #2 for his in-depth review of our manuscript.  

Reviewer #3 (Public Review):

The major claim from the paper is the dependence of two factors that determine the polymerization of MreB from a Gram-positive, thermophilic bacteria 1) The role of nucleotide hydrolysis in driving the polymerization. 2) Lipid bilayer as a facilitator/scaffold that is required for hydrolysis-dependent polymerization. These two conclusions are contrasting with what has been known until now for the MreB proteins that have been characterized in vitro. The experiments performed in the paper do not completely justify these claims as elaborated below.

We understand the reviewer’ concerns in view of the existing literature on actin and Gram-negative MreBs. We may just be missing the optimal conditions for polymerisation in solution, while our phrasing gave the impression that polymers could never form in the absence of ATP or lipids. Our new data actually shows that MreBGs at higher concentration can assemble into bundle- and sheet-like structures in solution and in the presence of ADP/AMP-PNP. Pairs of filaments are however only observed in the presence of lipids for all conditions tested. As indicated in the answers to the global review comments, we have included our new data in the manuscript, revised our conclusions and claims about the lipid requirement and expanded on these points in the Discussion.

Major comments:

1) No observation of filaments in the absence of lipid monolayer can also be accounted due to the higher critical concentration of polymerization for MreBGS in that condition. It is seen that all the negative staining without lipid monolayer condition has been performed at a concentration of 0.05 mg/mL. It is important to check for polymerization of the MreBGS at higher concentration ranges as well, in order to conclusively state the requirement of lipids for polymerization.

Response 3.1. 0.05 mg/ml (1.3µM) is our standard condition, and our leeway was limited by the rapid aggregation observed at higher MreB concentrations, as indicated in the text. We have now tested as well 0.25 mg/ml (6.5 µM - the maximum concentration possible before major aggregation occurs in our experimental conditions). At this higher concentration, we see some sheet-like structures in solution, confirming a requirement of a higher concentration of MreB for polymerization in these conditions (see the answers to the global review comments for more details)

We thank the reviewer for pushing us to address this point. We have revised our conclusions accordingly.

2) The absence of filaments for the non-hydrolysable conditions in the lipid layer could also be because the filaments that might have formed are not binding to the planar lipid layer, and not necessarily because of their inability to polymerize.

Response 3.2. This is a fair point. To test the possibility that polymers would form but would not bind to the lipid layer we have now added additional semi-quantitative EM controls (for both the non-hydrolysable ATP analogs and the three ‘membrane binding’ deletion mutants) testing polymerization in solution (without lipids) and also using plasma-treated grids. These showed that in our standard polymerization conditions, virtually no polymers form in solution (Fig. 3-S1B and Fig. 4-S4A). Albeit at very low frequency, some dual protofilaments were however detected in the presence of ADP or AMP-PNP at the high MreB concentration (Fig. 3-S1D). At this high MreB concentration, the sheet-like structures occasionally observed in solution in the presence of ATP were frequent in the presence of ADP and very frequent in the presence of AMP-PNP (Fig. 3-S2B). We have revised our conclusions on the basis of these new data: MreBGs can form polymeric assemblies in solution and in the absence of ATP hydrolysis at a higher critical concentration than in the presence of ATP and lipids.

See the answers to the global review comments (point 2) and Response 2.3C to reviewer #2 for more details.

3) Given the ATPase activity measurements, it is not very convincing that ATP rather than ADP will be present in the structure. The ATP should have been hydrolysed to ADP within the structure. The structure is now suggestive that MreB is not capable of hydrolysis, which is contradictory to the ATP hydrolysis data.

Response 3.3. We thank the reviewer for her insightful remarks about the MreB-ATP crystal structure. The electron density map clearly demonstrates the presence of 3 phosphates. However, as suggested by the reviewer, the density which was attributed to a Mg2+ ion was to be interpreted as a water molecule. The absence of Mg2+ in the crystal could thus explain why the ATP had not been hydrolyzed.

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Author Response:

Reviewer #2 (Public Review):

This work uses a throughput continuous culture system with simplified soil microbial communities to investigate how diversity-disturbance relationships (DDRs) change with different disturbance "intensities" (here, defined as mortality rate or dilution rate in a continuous system) and "frequencies" (here, defined as the number of dilution events that occur per day to achieve the desired mortality rate). Understanding the mechanisms that support different DDR is an ongoing and urgent need in ecology and ecosystem sciences because of the pressing need to predict and manage systems given climate and land-use disturbances.

A major strength of the work is a blending of modeling and empirical approaches. It includes an ambitiously-designed study that uses a controlled, high-throughput microbial community experimental system to observe disturbance outcomes and uses those observations to build their proposed quantitative framework. The figures are informative and framework is explained clearly. The authors propose and name a new mechanism, "niche-flip" that describes resource competition at varying disturbance "intensities" - this is an interesting proposal and I suggest that it is explored more fully as a potential mechanism (see weaknesses).

Weaknesses of the work are the use of definitions that are generally inconsistent with the disturbance ecology literature, and the inability to separate the disturbance event characteristic of "intensity" from the biological outcome of mortality. The authors conclude that DDRs are contextual, which is supported by their modeling and data, but I suggest that they consider that diversity as an outcome in itself may not be the most informative metric of what mechanism(s) drive context-specific outcomes. The authors have a lot of compositional data that could also be examined to understand whether their "niche-flip" mechanism is supported.

This work is likely to advance our understanding of the myriad of outcomes of DDR and what potential mechanisms may support those DDR in natural ecosystems.

Thank you for your kind words and careful review of our manuscript. We are pleased you appreciate both the experiments and the modeling work, and that you are intrigued by the findings and the niche flip mechanism.

Major comments:

Comment 1. Ecological definitions and interdependence of disturbance outcomes/attributes

The authors define disturbance "intensity" as the average mortality rate but claim that this is a disturbance characteristic. However, mortality rate is not a characteristic of a disturbance event, but rather an effect/outcome of a disturbance on the biological community. The key distinction is that disturbance characteristics (also called traits or aspects) are defined relative to the environment, while disturbance outcomes (also called effects, impacts, or responses) are defined relative to the biology of interest, in this case a microbial community. So, changes in diversity of the community, as a result of a disturbance, is a biological outcome of the disturbance. An average mortality rate, what the authors call "intensity" (L40) would be such an outcome.

Thank you for this excellent point. We have revised the introduction to make this distinction, reproduced here for convenience:

"Accordingly, there have been many efforts aimed at understanding the role of environmental disturbances, which are perturbations to the state of an environment. These disturbances are of ecological interest for the impact they have on a community, for example, by bringing about mortality of organisms and a reduction of biomass of a community."

The authors' definition of "intensity" is not in agreement with the disturbance ecology literature, including the references cited in this current work. For example, in reference #18 (Miller et al. 2011 PNAS) disturbance aspects include intensity, timing, duration, extent, and interval. Specifically, Miller et al. 2011 defined intensity as the magnitude of the disturbance (e.g., a flood's maximum stage). Notably, Miller's definition of intensity is more aligned with the author's definition of "fluctuation," which the authors define as the "magnitude of deviations from the average". In the current work, the disturbance "event" cannot be separated from the biological outcome because of the nature of the continuous culture system. The system is not being disturbed with, for example, a change in pH or salinity or another environmental variable that results in microbial mortality, but rather the loss of viable members from the community through control of the flow-through. So, the mortality is both the precisely controlled disturbance "event" and "outcome" in the continuous culture.

To summarize, the premise of the article is confusing, because one of the two disturbance "characteristics" considered is, rather a disturbance outcome. This may seem like mincing words and to each paper its own definitions, but because this work seeks to reconcile DDRs as reported across many studies, and because many of the previous ecology studies that have investigated or reported DDRs are not using analogous terms, the work could further confusion rather than serve as a reconciliation. When different definitions are applied that mix disturbance aspects with biological outcomes of disturbance, readers will have to work hard to understand this work in context with the existing literature. I suggest revising the introductory section to be consistent in terminology with the ecology literature and to be framed not only as disturbance characteristics, but also outcomes. I also suggest adding discussion of how an inability to distinguish disturbance event from outcome may influence interpretation of this work and its broader application. I suggest adding clarification/discussion of "how intensity and fluctuations interact" (e.g. L200): as the authors define intensity and fluctuation of the disturbance event, intensity is not independent of the biological disturbance outcome of mortality in the given model system. So, how the two "disturbance components interact" is not able to be examined independently from the biological outcome (mortality, resulting diversity).

These are also critical points. First, we will address the choice of terminology (re: Miller et al) and, second, the equivalence between disturbance and outcome in continuous culture.

We agree that careful use of terminology is important for understanding our work in context of the literature. Accordingly, we have replaced our characteristics “intensity” and “fluctuation” with “mean intensity” and “frequency” throughout the paper. We have also added more examples through the results section to indicate how mean intensity, frequency, and maximum dilution rates (during disturbance events) are related.

"To determine whether the effects of disturbance on diversity are truly fluctuation-dependent15, a disturbance should ideally be decomposed into distinct components of mean intensity (e.g. time-averaged disturbance magnitude) and frequency (e.g. temporal profile of fluctuations)."

The direct connection between disturbance and mortality in a continuous culture system under dilution disturbances is a critical aspect of our experimental design, because we wanted to compare disturbance outcomes that varied in temporal features (in Miller et al terms, intensity/magnitude vs frequency/timing) while holding mortality equal. In continuous culture this may be achieved by controlling dilution rate and frequency, but you are correct that other classes of natural disturbances such as pH or salinity changes may have different effects on community members. As a first step towards investigating these effects, we had included analyses with non-equal mortality rates (Appendix figure 4). We have now edited the introduction and discussion to emphasize that the equivalence between disturbance event and disturbance outcome is a feature specific to continuous culture.

Introduction

"Dilution is perhaps the most common choice for a laboratory disturbance, as it causes species-independent mortality and replenishes the system with fresh nutrients, reminiscent of flow in soil, aquatic, or gut microbiomes. Unlike disturbances with indirect biological impacts (such as pH, temperature, or osmolarity disturbances), there is a direct link between the dilution disturbance event (removal of culture volume) and the biological outcome (mortality of community members)."

Discussion

"We also note however, that these types of disturbances do not share the direct link between environmental change and biological outcome that is characteristic of dilution disturbance, so the impact may be less clear."

Comment 2: Compositional evidence for the proposed "niche flip" mechanism and suggestion for deeper consideration of population-level response to disturbance outcomes that collectively contribute to emergent diversity values.

Regarding the "niche flip" - it is unclear whether there is compositional evidence for any swap in niche preference/space among particular community members. Figure S8 may offer evidence, but I could not deduce it from the busy bar charts. Could population/ASV level analysis be conducted on each member to assess their dynamics and ask whether the dynamics support the proposed niche-flip as a DDR mechanism?

This is a very interesting suggestion. As suggested, we could extract the relative preferences of different ASVs from composition data to test a prediction about changes in the composition resulting from niche flip. To make such a prediction, we’d need the Monod growth parameters of the species on relevant resources. We began collecting this data (see Figure 3 – figure supplement 4) but found it challenging to measure these parameters on defined media sources. Furthermore, since we elected to run our main experiments in a complex media that could potentially support diverse communities (as opposed to minimal medias which produce simple communities, see Goldford et al Science 2018) we cannot link Monod growth parameters in this media to particular resources. Subsequent experiments with defined species with measured Monod parameters in defined media would enable us to make and test predictions. These are sizeable experiments that we do not believe are in the scope of the present work. Without a testable prediction, we do not believe species or ASV level analysis to be particularly informative on its own.

Related, there seems to be possible evidence of a "fluctuation" rate threshold, after which there is a major compositional shift in the microbial community. Consider Figure 3: At all "intensities", there is a shift in microbial community composition between "fluctuation" rates of 4/day and 16/day (3d, Fig S8). This threshold/shift is not also apparent in the Shannon diversity in Fig 3f. This could be an example in which diversity as a metric in itself is not as informative/useful outcome for disturbance responses, as identical Shannon diversity values can result from different community compositions that are themselves the outcomes of different mechanisms. I see from the PCoAs (Fig S9) that the authors were exploring potential compositional clustering by day, frequency, and dilution - the most "obvious" clustering to the eye is indeed by "frequency" and between 4/day and 16/day (red/blue separation along both axes, which also supports a potential threshold/shift. Generally, it would have been good to report statistical tests (e.g., PERMANOVA or equivalent) for these PCoA categories (where it makes sense, nested and term interactions as well) - is there statistical support for compositional threshold shift between 4/16?

Thank you for these suggestions. Indeed, by eye and by the PCoA plots, there seems to be a significant difference in composition that separate the low-frequency (1/day & 4/day) from the high-frequency (16/day & Constant) conditions. We calculated pairwise distances between Day 6 samples grouped by A) dilution frequency, B) mean dilution rate, or C) combinations of dilution rate and frequency. Using these distances to perform PERMANOVA tests, we find significant differences between cultures with different frequencies, but not for cultures with different dilution rates. For combinations, we found several pairs with differences that were significant only before correction for false-discovery rate. Distances between low-frequency (1/day & 4/day) conditions are much smaller than between low-frequency and high-frequency groups, or between the high-frequency groups. We have now included this as Figure 3 – figure supplement 9 and have summarized the results in the main text, reproduced below for convenience:

"PERMANOVA statistical analysis of endpoint compositions confirmed that dilution frequency (but not mean dilution rate) had a significant effect on composition (Figure 3 – figure supplement 9). Despite separation between conditions in PCoA of endpoint compositions (Figure 3 – figure supplement 9), PERMANOVA analysis of dilution rate and frequency combinations did not yield significant values after correcting for false discovery rate."

Reviewer #3 (Public Review):

This manuscript focuses on the relationship between diversity and disturbance. The authors study this relationship in experimental microbial communities. These communities as subject to different levels of disturbance, which is identified as the dilution rate. The authors find a non-monotonic relationship between diversity and dilution rate. In presence of temporal fluctuations, the non-monotonic relationship becomes less evident, disappearing for strong enough fluctuations. The experimental findings are well explained by a consumer-resource model with Monod response.

The results of the paper are a very interesting combination of experimental and theoretical work. The manuscript is well written and easy to follow.

Experiments. The data support the main result of the paper. The U-shaped disturbance-diversity relationship (DDR) is robust (e.g., independent of the measure of diversity). The experimental setup is innovative.

Theory. A main strength of the manuscript is the clarity in which the model reproduces the experimental data. It is also interesting that alternative models (Lotka-Volterra and consumer-resource with linear response) do not reproduce the data, therefore indicating the relevance of the data themselves. The main weakness of the paper is that, in the end, the mechanism behind the non-monotonicity of the DDR is not completely clear. The authors discuss how it emerges with two species and two resources in presence of a trade-off between maximal growth rate and resource-limited growth rate: at low dilution rate, the species with high maximal growth rate wins, while at high dilution rate the one with resource-limited growth rate dominates. This mechanism is clear with two species (in which diversity can transition between 2 and 1). It is unclear what happens for more species and resources. In particular, the role of the tradeoff --- which is central in the pairwise competition case --- is unclear: the U-shapes relationship is observed also in absence of the tradeoff for multispecies communities.

Thank you for your enthusiasm about our work and your careful review of our manuscript. We are pleased you appreciate the concordance between experiment and model in our study.

Author Response:

Reviewer #1:

The submitted manuscript 'Distinct higher-order representations of natural sounds in human and ferret auditory cortex' by Landemard and colleagues seeks to investigate the neural representations of sound in the ferret auditory cortex. Specifically, they examine the stages of processing via manipulating the complexity and sound structure of stimuli. The authors create synthetic auditory stimuli that are statistically equivalent to natural sounds in their cochlear representation, temporal modulation structure, spectral modulation structure, and spectro-temporal modulation structure. The authors use functional ultrasound imaging (fUS) which allowed for the measurement of the hemodynamic signal at much finer spatial scales than fMRI, making it particularly suitable for the ferret. The authors then compare their results to work done in humans that has previously been published (e.g. Norman-Haignere and McDermott, 2018) and find that: 1. While human non-primary auditory cortex demonstrates a significant difference between natural speech/music sounds and their synthetic counterparts, the ferret non-primary auditory cortex does not. 2. For each sound manipulation in humans, the dissimilarity increases as the distance from the primary auditory cortex increases, whereas for ferrets it does not. 3. While ferrets behaviorally respond to con-specific vocalizations, the ferret auditory cortex does not demonstrate the same hierarchical processing stream as humans do.

Overall, I find the approach (especially the sound manipulations) excellent and the overall finding quite intriguing. My only concern, is that it is essentially a null-result. While this result will be useful to the literature, there is always the concern that a lack of finding could also be due to other factors.

Thank you for taking the time to carefully read our manuscript. We have done our best to address all of your questions and concerns, which has improved the paper.

We note that our finding differs from a typical null result in two ways. First, our key finding is that responses to natural and synthetic sounds are closely matched throughout primary and non-primary auditory cortex. Unlike a typical null result, this finding cannot be due to a noisy measure, since if our data were noisy, we would not have observed any correspondence between natural and synthetic sounds. Second, we have a clear prediction from humans as to what we should observe if the organization were similar: matched responses in primary auditory cortex and divergent responses in non-primary auditory cortex. Our data clearly demonstrate that this prediction is wrong, for all of the reasons noted in our general response above. In essence, what we are showing is that there is a region by species interaction in the similarity of responses to natural vs. synthetic sounds (as reflected by a significant difference in slopes between species, see our response above). We have investigated and ruled out all of the alternative explanations we can think of for this interaction (e.g. differences in SNR or spatial resolution) and are left with the conclusion that there is a meaningful difference in functional organization between humans and ferrets. If there are any additional concerns you have, we would be happy to address them.

Major points:

1) What if the stages in the ferret are wrong? The authors use 4 different manipulations thought to reflect key elements of sound structure and/or the relevant hierarchy of the processing stages of the auditory cortex, but it's possible that the dimensions in the ferret auditory cortex are along a different axis than spectro/temporal modulations. While I do not expect the authors to attempt every possible axis, it would be beneficial to discuss.

Thank you for raising this question. We now directly address this question in the Discussion (page 11):

"Our findings show that a prominent signature of hierarchical functional organization present in humans – preferential responses for natural vs. spectrotemporal structure – is largely absent in ferret auditory cortex. But this finding does not imply that there is no functional differentiation between primary and non-primary regions in ferrets. For example, ferret non-primary regions show longer latencies, greater spectral integration bandwidths, and stronger task-modulated responses compared with primary regions (Elgueda et al., 2019). The fact that we did not observe differences between primary and non-primary regions is not because the acoustic features manipulated are irrelevant to ferret auditory cortex, since our analysis shows that matching frequency and modulation statistics is sufficient to match the ferret cortical response, at least as measured by ultrasound. Indeed, if anything, it appears that modulation features are more relevant to the ferret auditory cortex since these features appear to drive responses throughout primary and non-primary regions, unlike human auditory cortex where we only observed strong, matched responses in primary regions."

2) For the ferret vocalizations, it is possible that a greater N would allow for a clearer picture of whether or not the activation is greater than speech/music? While it is clear that any difference would be subtle and probably require a group analysis, this would help settle this result/issue (at least at the group level).

Below we plot the distribution of NSE values for ferret vocalizations, speech, and music, averaged across all of auditory cortex and plotted separately for each ferret tested (panel A). As is evident, we observe larger NSE values for ferret vocalizations in one animal (p < 0.01, Wilcoxon test), but no difference in the other two (p > 0.55). When we perform a group analysis, averaging across all three animals, we do not observe any significant difference between the categories (panel B) (p = 0.27). Moreover, even for ferret vocalizations, NSE values were similar throughout primary and non-primary regions, and this was true in all three animals tested (panel C). Given these data, we do not believe our study provides evidence for a difference between ferret vocalizations and other categories. Panel A is plotted in the revised Figure 4 - figure supplement 1E. The distance-to-PAC curves (panel C) and the corresponding slopes are plotted in Figure 4D-E.

Individual and group analyses of the difference between natural and spectrotemporally matched synthetic sounds, broken down by sound category. A, The NSE between natural and synthetic sounds plotted separately for each animal and sound category. NSE values have been averaged across all of auditory cortex. Each circle represents a single pair of natural/synthetic sounds. We find that the NSE values are larger for ferret vocalizations in Ferret A, but this effect is not present in Ferret T or C ( indicates p < 0.005, Wilcoxon test). B, NSE values averaged across animals. C, NSEs for ferret vocalizations, plotted as a function of distance to primary auditory cortex (PAC). Figure shows both individual subject (thin pink lines) and group-averaged data (thick pink line).

Below, we have reproduced the relevant paragraph of the results where we discuss these and other related findings (page 6):

"To directly test if ferrets showed preferential responses to natural vs. synthetic ferret vocalizations, we computed maps plotting the average difference between natural vs. synthetic sounds for different categories, using data from both Experiments I and II (Figure 4C). We also separately measured the NSE for sounds from different categories, again plotting NSE values as a function of distance to PAC (Figure 4D-E). The differences that we observed between natural and synthetic sounds were small and scattered throughout primary and non-primary auditory cortex, even for ferret vocalizations. In one animal, we observed significantly larger NSE values for ferret vocalizations compared with speech and music (Ferret A, Mdvoc = 0.137 vs MdSpM = 0.042, Wilcoxon rank-sum test: T = 1138, z = 3.29, p < 0.01). But this difference was not present in the other two ferrets tested (p > 0.55) and was also not present when we averaged NSE values across animals (Mdvoc = 0.053 vs MdSpM = 0.033, Wilcoxon rank- sum test: T = 1016, z = 1.49, p = 0.27). Moreover, the slope of the NSE vs. distance-to- PAC curve was near 0 for all animals and sound categories, even for ferret vocalizations, and was substantially lower than the slopes measured in all 12 human subjects (Figure 4F) (vocalizations in ferrets vs. speech in humans: p < 0.001 via a sign test; speech in ferrets vs. speech in humans: p < 0.001). In contrast, human cortical responses were substantially larger for natural vs. synthetic speech and music, and these response enhancements were concentrated in distinct non-primary regions (lateral for speech and anterior/posterior for music) and clearly different from those for other natural sounds (Figure 4C). Thus, ferrets do not show any of the neural signatures of higher-order sensitivity that we previously identified in humans (large effect size, spatially clustered responses, and a clear non-primary bias), even for con- specific vocalizations."

3) Relatedly, did the magnitude of this effect increase outside the auditory cortex?

We did not record outside of auditory cortex. Unlike fMRI, it is not easy to get whole-brain coverage using current fUS probes. Since our goal was to test if ferret auditory cortex showed similar organization as human auditory cortex, we focused our data collection on auditory regions. We have clarified this point in the Methods (page 13):

"fUS data are collected as a series of 2D images or ‘slices’. Slices were collected in the coronal plane and were spaced 0.4 mm apart. The slice plane was varied across sessions in order to cover the region-of-interest which included both primary and non- primary regions of auditory cortex. We did not collect data from non-auditory regions due to limited time/coverage."

4) It would be useful to have a measure of the noise floor for each plot and/or species for NSE analyses. This would make it easier to distinguish whether, for instance, in 2A-D, an NSE of 0.1 (human primary) vs. an NSE of 0.042 (ferret primary) should be interpreted as a bit more than double, or both close to the noise floor (which is what I presume).

All of our NSE measures are noise-corrected such that the effective floor is zero (noise- correction provides an estimate of what the NSE value would be given perfectly reliable measurements). The only exception are cases where we plot the NSE values for example voxels/ROIs (Figure 2A-D, Figure 2 - figure supplement 1), in which case we plot both the raw NSE values along with the noise floor, which is given by the test-retest NSE of the measurements. To address your comment, we have included a supplemental plot (Figure 2 - figure supplement 3) that shows the median uncorrected NSE as a function of distance to primary auditory cortex, along with the noise floor given by the reliability of the measurements. The figure is reproduced below.

Figure 2 - figure supplement 3. Uncorrected NSE values. This figure plots the uncorrected NSE between natural and synthetic sounds as a function of distance to primary auditory cortex (PAC). The test-retest NSE value, which provides a noise floor for the natural vs. synthetic NSE, is plotted below each set of curves using dashed lines. Each thin line corresponds to a single ferret (gray) or a single human subject (gold). Thick lines show the average across all subjects. Format is the same as Figure 2F.

We have clarified this important detail in the Results (page 4):

"We used the test-retest reliability of the responses to noise-correct the measured NSE values such that the effective noise floor given the reliability of the measurements is zero."

Reviewer #2:

Landemard et al. compare the response properties of primary vs. non-primary auditory cortex in ferrets with respect to natural and model-matched sounds, using functional ultrasound imaging. They find that responses do not differentiate between natural and model-matched sounds across ferret auditory cortex; in contrast, by drawing on previously published data in humans where Norman-Haignere & McDermott (2018) showed that non-primary (but not primary) auditory cortex differentiates between natural and model-matched sounds, the authors suggest that this is a defining distinction between human and non-human auditory cortex. The analyses are conducted well and I appreciate the authors including a wealth of results, also split up for individual subjects and hemispheres in supplementary figures, which helps the reader get a better idea of the underlying data.

Overall, I think the authors have completed a very nice study and present interesting results that are applicable to the general neuroscience community. I think the manuscript could be improved by using different terminology ('sensitivity' as opposed to 'selectivity'), a larger subject pool (only 2 animals), and some more explanation with respect to data analysis choices.

Many thanks for your thoughtful critiques and comments. We have attempted to address all of them, which has improved the manuscript.

Author Response

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

eLife assessment

This important paper exploits new cryo-EM tomography tools to examine the state of chromatin in situ. The experimental work is meticulously performed and convincing, with a vast amount of data collected. The main findings are interpreted by the authors to suggest that the majority of yeast nucleosomes lack a stable octameric conformation. Despite the possibly controversial nature of this report, it is our hope that such work will spark thought-provoking debate, and further the development of exciting new tools that can interrogate native chromatin shape and associated function in vivo.

We thank the Editors and Reviewers for their thoughtful and helpful comments. We also appreciate the extraordinary amount of effort needed to assess both the lengthy manuscript and the previous reviews. Below, we provide our point-by-point response in bold blue font. Nearly all comments have been addressed in the revised manuscript. For a subset of comments that would require us to speculate, we have taken a conservative approach because we either lack key information or technical expertise: Instead of adding the speculative replies to the main text, we think it is better to leave them in the rebuttal for posterity. Readers will thereby have access to our speculation and know that we did not feel confident enough to include these thoughts in the Version of Record.

Reviewer #1 (Public Review):

This manuscript by Tan et al is using cryo-electron tomography to investigate the structure of yeast nucleosomes both ex vivo (nuclear lysates) and in situ (lamellae and cryosections). The sheer number of experiments and results are astounding and comparable with an entire PhD thesis. However, as is always the case, it is hard to prove that something is not there. In this case, canonical nucleosomes. In their path to find the nucleosomes, the authors also stumble over new insights into nucleosome arrangement that indicates that the positions of the histones is more flexible than previously believed.

Please note that canonical nucleosomes are there in wild-type cells in situ, albeit rarer than what’s expected based on our HeLa cell analysis and especially the total number of yeast nucleosomes (canonical plus non-canonical). The negative result (absence of any canonical nucleosome classes in situ) was found in the histone-GFP mutants.

Major strengths and weaknesses:

Personally, I am not ready to agree with their conclusion that heterogenous non-canonical nucleosomes predominate in yeast cells, but this reviewer is not an expert in the field of nucleosomes and can't judge how well these results fit into previous results in the field. As a technological expert though, I think the authors have done everything possible to test that hypothesis with today's available methods. One can debate whether it is necessary to have 35 supplementary figures, but after working through them all, I see that the nature of the argument needs all that support, precisely because it is so hard to show what is not there. The massive amount of work that has gone into this manuscript and the state-of-the art nature of the technology should be warmly commended. I also think the authors have done a really great job with including all their results to the benefit of the scientific community. Yet, I am left with some questions and comments:

Could the nucleosomes change into other shapes that were predetermined in situ? Could the authors expand on if there was a structure or two that was more common than the others of the classes they found? Or would this not have been found because of the template matching and later reference particle used?

Our best guess (speculation) is that one of the class averages that is smaller than the canonical nucleosome contains one or more non-canonical nucleosome classes. However, we do not feel confident enough to single out any of these classes precisely because we do not yet know if they arise from one non-canonical nucleosome structure or from multiple – and therefore mis-classified – non-canonical nucleosome structures (potentially with other non-nucleosome complexes mixed in). We feel it is better to leave this discussion out of the manuscript, or risk sending the community on wild goose chases.

Our template-matching workflow uses a low-enough cross-correlation threshold that any nucleosome-sized particle (plus minus a few nanometers) would be picked, which is why the number of hits is so large. So unless the noncanonical nucleosomes quadrupled in size or lost most of their histones, they should be grouped with one or more of the other 99 class averages (WT cells) or any of the 100 class averages (cells with GFP-tagged histones). As to whether the later reference particle could have prevented us from detecting one of the non-canonical nucleosome structures, we are unable to tell because we’d really have to know what an in situ non-canonical nucleosome looks like first.

Could it simply be that the yeast nucleoplasm is differently structured than that of HeLa cells and it was harder to find nucleosomes by template matching in these cells? The authors argue against crowding in the discussion, but maybe it is just a nucleoplasm texture that side-tracks the programs?

Presumably, the nucleoplasmic “side-tracking” texture would come from some molecules in the yeast nucleus. These molecules would be too small to visualize as discrete particles in the tomographic slices, but they would contribute textures that can be “seen” by the programs – in particular RELION, which does the discrimination between structural states. We are not sure what types of density textures would side-track RELION’s classification routines.

The title of the paper is not well reflected in the main figures. The title of Figure 2 says "Canonical nucleosomes are rare in wild-type cells", but that is not shown/quantified in that figure. Rare is comparison to what? I suggest adding a comparative view from the HeLa cells, like the text does in lines 195-199. A measure of nucleosomes detected per volume nucleoplasm would also facilitate a comparison.

Figure 2’s title is indeed unclear and does not align with the paper’s title and key conclusion. The rarity here is relative to the expected number of nucleosomes (canonical plus non-canonical). We have changed the title to:

“Canonical nucleosomes are a minority of the expected total in wild-type cells”.

We would prefer to leave the reference to HeLa cells to the main text instead of as a figure panel because the comparison is not straightforward for a graphical presentation. Instead, we now report the total number of nucleosomes estimated for this particular yeast tomogram (~7,600) versus the number of canonical nucleosomes classified (297; 594 if we assume we missed half of them). This information is in the revised figure legend:

“In this tomogram, we estimate there are ~7,600 nucleosomes (see Methods on how the calculation is done), of which 297 are canonical structures. Accounting for the missing disc views, we estimate there are ~594 canonical nucleosomes in this cryolamella (< 8% the expected number of nucleosomes).”

If the cell contains mostly non-canonical nucleosomes, are they really non-canonical? Maybe a change of language is required once this is somewhat sure (say, after line 303).

This is an interesting semantic and philosophical point. From the yeast cell’s “perspective”, the canonical nucleosome structure would be the form that is in the majority. That being said, we do not know if there is one structure that is the majority. From the chromatin field’s point of view, the canonical nucleosome is the form that is most commonly seen in all the historical – and most contemporary – literature, namely something that resembles the crystal structure of Luger et al, 1997. Given these two lines of thinking, we added the following clarification as lines 312 – 316:

“At present, we do not know what the non-canonical nucleosome structures are, meaning that we cannot even determine if one non-canonical structure is the majority. Until we know the non-canonical nucleosomes’ structures, we will use the term non-canonical to describe all the nucleosomes that do not have the canonical (crystal) structure.”

The authors could explain more why they sometimes use conventional the 2D followed by 3D classification approach and sometimes "direct 3-D classification". Why, for example, do they do 2D followed by 3D in Figure S5A? This Figure could be considered a regular figure since it shows the main message of the paper.

Since the classification of subtomograms in situ is still a work in progress, we felt it would be better to show one instance of 2-D classification for lysates and one for lamellae. While it is true that we could have presented direct 3-D classification for the entire paper, we anticipate that readers will be interested to see what the in situ 2-D class averages look like.

The main message is that there are canonical nucleosomes in situ (at least in wild-type cells), but they are a minority. Therefore, the conventional classification for Figure S5A should not be a main figure because it does not show any canonical nucleosome class averages in situ.

Figure 1: Why is there a gap in the middle of the nucleosome in panel B? The authors write that this is a higher resolution structure (18Å), but in the even higher resolution crystallography structure (3Å resolution), there is no gap in the middle.

There is a lower concentration of amino acids at the middle in the disc view; unfortunately, the space-filling model in Figure 1A hides this feature. The gap exists in experimental cryo-EM density maps. See Author response image 1 for an example (pubmed.ncbi.nlm.nih.gov/29626188). The size of the gap depends on the contour level and probably the contrast mechanism, as the gap is less visible in the VPP subtomogram averages. To clarify this confusing phenomenon, we added the following lines to the figure legend:

“The gap in the disc view of the nuclear-lysate-based average is due to the lower concentration of amino acids there, which is not visible in panel A due to space-filling rendering. This gap’s visibility may also depend on the contrast mechanism because it is not visible in the VPP averages.”

Author response image 1.

Reviewer #2 (Public Review):

Nucleosome structures inside cells remain unclear. Tan et al. tackled this problem using cryo-ET and 3-D classification analysis of yeast cells. The authors found that the fraction of canonical nucleosomes in the cell could be less than 10% of total nucleosomes. The finding is consistent with the unstable property of yeast nucleosomes and the high proportion of the actively transcribed yeast genome. The authors made an important point in understanding chromatin structure in situ. Overall, the paper is well-written and informative to the chromatin/chromosome field.

We thank Reviewer 2 for their positive assessment.

Reviewer #3 (Public Review):

Several labs in the 1970s published fundamental work revealing that almost all eukaryotes organize their DNA into repeating units called nucleosomes, which form the chromatin fiber. Decades of elegant biochemical and structural work indicated a primarily octameric organization of the nucleosome with 2 copies of each histone H2A, H2B, H3 and H4, wrapping 147bp of DNA in a left handed toroid, to which linker histone would bind.

This was true for most species studied (except, yeast lack linker histone) and was recapitulated in stunning detail by in vitro reconstitutions by salt dialysis or chaperone-mediated assembly of nucleosomes. Thus, these landmark studies set the stage for an exploding number of papers on the topic of chromatin in the past 45 years.

An emerging counterpoint to the prevailing idea of static particles is that nucleosomes are much more dynamic and can undergo spontaneous transformation. Such dynamics could arise from intrinsic instability due to DNA structural deformation, specific histone variants or their mutations, post-translational histone modifications which weaken the main contacts, protein partners, and predominantly, from active processes like ATP-dependent chromatin remodeling, transcription, repair and replication.

This paper is important because it tests this idea whole-scale, applying novel cryo-EM tomography tools to examine the state of chromatin in yeast lysates or cryo-sections. The experimental work is meticulously performed, with vast amount of data collected. The main findings are interpreted by the authors to suggest that majority of yeast nucleosomes lack a stable octameric conformation. The findings are not surprising in that alternative conformations of nucleosomes might exist in vivo, but rather in the sheer scale of such particles reported, relative to the traditional form expected from decades of biochemical, biophysical and structural data. Thus, it is likely that this work will be perceived as controversial. Nonetheless, we believe these kinds of tools represent an important advance for in situ analysis of chromatin. We also think the field should have the opportunity to carefully evaluate the data and assess whether the claims are supported, or consider what additional experiments could be done to further test the conceptual claims made. It is our hope that such work will spark thought-provoking debate in a collegial fashion, and lead to the development of exciting new tools which can interrogate native chromatin shape in vivo. Most importantly, it will be critical to assess biological implications associated with more dynamic - or static forms- of nucleosomes, the associated chromatin fiber, and its three-dimensional organization, for nuclear or mitotic function.

Thank you for putting our work in the context of the field’s trajectory. We hope our EMPIAR entry, which includes all the raw data used in this paper, will be useful for the community. As more labs (hopefully) upload their raw data and as image-processing continues to advance, the field will be able to revisit the question of non-canonical nucleosomes in budding yeast and other organisms. 

Reviewer #1 (Recommendations For The Authors):

The manuscript sometimes reads like a part of a series rather than a stand-alone paper. Be sure to spell out what needs to be known from previous work to read this article. The introduction is very EM-technique focused but could do with more nucleosome information.

We have added a new paragraph that discusses the sources of structural variability to better prepare readers, as lines 50 – 59:

“In the context of chromatin, nucleosomes are not discrete particles because sequential nucleosomes are connected by short stretches of linker DNA. Variation in linker DNA structure is a source of chromatin conformational heterogeneity (Collepardo-Guevara and Schlick, 2014). Recent cryo-EM studies show that nucleosomes can deviate from the canonical form in vitro, primarily in the structure of DNA near the entry/exit site (Bilokapic et al., 2018; Fukushima et al., 2022; Sato et al., 2021; Zhou et al., 2021). In addition to DNA structural variability, nucleosomes in vitro have small changes in histone conformations (Bilokapic et al., 2018). Larger-scale variations of DNA and histone structure are not compatible with high-resolution analysis and may have been missed in single-particle cryo-EM studies.”

Line 165-6 "did not reveal a nucleosome class average in..". Add "canonical", since it otherwise suggests there were no nucleosomes.

Thank you for catching this error. Corrected.

Lines 177-182: Why are the disc views missed by the classification analysis? They should be there in the sample, as you say.

We suspect that RELION 3 is misclassifying the disc-view canonical nucleosomes into the other classes. The RELION developers suspect that view-dependent misclassification arises from RELION 3’s 3-D CTF model. RELION 4 is reported to be less biased by the particles’ views. We have started testing RELION 4 but do not have anything concrete to report yet.

Line 222: a GFP tag.

Fixed.

Line 382: "Note that the percentage .." I can't follow this sentence. Why would you need to know how many chromosome's worth of nucleosomes you are looking at to say the percentage of non-canonical nucleosomes?

Thank you for noticing this confusing wording. The sentence has been both simplified and clarified as follows in lines 396 – 398:

“Note that the percentage of canonical nucleosomes in lysates cannot be accurately estimated because we cannot determine how many nucleosomes in total are in each field of view.”

Line 397: "We're not implying that..." Please add a sentence clearly stating what you DO mean with mobility for H2A/H2B.

We have added the following clarifying sentence in lines 412 – 413:

“We mean that H2A-H2B is attached to the rest of the nucleosome and can have small differences in orientation.”

Line 428: repeated message from line 424. "in this figure, the blurring implies.."

Redundant phrase removed.

Line 439: "on a HeLa cell" - a single cell in the whole study?

Yes, that study was done on a single cell.

A general comment is that the authors could help the reader more by developing the figures and making them more pedagogical, a list of suggestions can be found below.

Thank you for the suggestions. We have applied all of them to the specific figure callouts and to the other figures that could use similar clarification.

Figure 2: Help the reader by avoiding abbreviations in the figure legend. VPP tomographic slice - spell out "Volta Phase Plate". Same with the term "remapped" (panel B) what does that mean?

We spelled out Volta phase plate in full and explained “remapped” the additional figure legend text:

“the class averages were oriented and positioned in the locations of their contributing subtomograms”.

Supplementary figures:

Figure S3: It is unclear what you mean with "two types of BY4741 nucleosomes". You then say that the canonical nucleosomes are shaded blue. So what color is then the non-canonical? All the greys? Some of them look just like random stuff, not nucleosomes.

“Two types” is a typo and has been removed and “nucleosomes” has been replaced with “candidate nucleosome template-matching hits” to accurately reflect the particles used in classification.

Figure S6: Top left says "3 tomograms (defocus)". I wonder if you meant to add the defocus range here. I have understood it like this is the same data as shown in Figure S5, which makes me wonder if this top cartoon should not be on top of that figure too (or exclusively there).

To make Figures S6 (and S5) clearer, we have copied the top cartoon from Figure S6 to S5.

Note that we corrected a typo for these figures (and the Table S7): the number of template-matched candidate nucleosomes should be 93,204, not 62,428.

The description in the parentheses (defocus) is shorthand for defocus phase contrast and was not intended to also display a defocus range. All of the revised figure legends now report the meaning of both this shorthand and of the Volta phase plate (VPP).

To help readers see the relationship between these two figures, we added the following clarifying text to the Figure S5 and S6 legends, respectively:

“This workflow uses the same template-matched candidate nucleosomes as in Figure S6; see below.”

“This workflow uses the same template-matched candidate nucleosomes as in Figure S5.”

Figure S7: In the first panel, it is unclear why the featureless cylinder is shown as it is not used as a reference here. Rather, it could be put throughout where it was used and then put the simulated EM-map alone here. If left in, it should be stated in the legend that it was not used here.

It would indeed be much clearer to show the featureless cylinder in all the other figures and leave the simulated nucleosome in this control figure. All figures are now updated. The figure legend was also updated as follows:

“(A) A simulated EM map from a crystal structure of the nucleosome was used as the template-matching and 3-D classification reference.”

Figure S18: Why are there classes where the GFP density is missing? Mention something about this in the figure legend.

We have appended the following speculations to explain the “missing” GFP densities:

“Some of the class averages are “missing” one or both expected GFP densities. The possible explanations include mobility of a subpopulation of GFPs or H2A-GFPs, incorrectly folded GFPs, or substitution of H2A for the variant histone H2A.Z.”

Reviewer #2 (Recommendations For The Authors):

My specific (rather minor) comments are the following:

1) Abstract:

yeast -> budding yeast.

All three instances in the abstract have been replaced with “budding yeast”.

It would be better to clarify what ex vivo means here.

We have appended “(in nuclear lysates)” to explain the meaning of ex vivo.

2) Some subtitles are unclear.

e.g., "in wild-type lysates" -> "wild-type yeast lysates"

Thank you for this suggestion. All unclear instances of subtitles and sample descriptions throughout the text have been corrected.

3) Page 6, Line 113. "...which detects more canonical nucleosomes." A similar thing was already mentioned in the same paragraph and seems redundant.

Thank you for noticing this redundant statement, which is now deleted.

4) Page 25, Line 525. "However, crowding is an unlikely explanation..." Please note that many macromolecules (proteins, RNAs, polysaccharides, etc.) were lost during the nuclei isolation process.

This is a good point. We have rewritten this paragraph to separate the discussion on technical versus biological effects of crowding, in lines 538 – 546:

“Another hypothesis for the low numbers of detected canonical nucleosomes is that the nucleoplasm is too crowded, making the image processing infeasible. However, crowding is an unlikely technical limitation because we were able to detect canonical nucleosome class averages in our most-crowded nuclear lysates, which are so crowded that most nucleosomes are butted against others (Figures S15 and S16). Crowding may instead have biological contributions to the different subtomogram-analysis outcomes in cell nuclei and nuclear lysates. For example, the crowding from other nuclear constituents (proteins, RNAs, polysaccharides, etc.) may contribute to in situ nucleosome structure, but is lost during nucleus isolation.”

5) Page 7, Line 126. "The subtomogram average..." Is there any explanation for this?

Presumably, the longer linker DNA length corresponds to the ordered portion of the ~22 bp linker between consecutive nucleosomes, given the ~168 bp nucleosome repeat length. We have appended the following explanation as the concluding sentence, lines 137 – 140:

“Because the nucleosome-repeat length of budding yeast chromatin is ~168 bp (Brogaard et al., 2012), this extra length of DNA may come from an ordered portion of the ~22 bp linker between adjacent nucleosomes.”

6) "Histone GFP-tagging strategy" subsection:

Since this subsection is a bit off the mainstream of the paper, it can be shortened and merged into the next one.

We have merged the “Histone GFP-tagging strategy” and “GFP is detectable on nucleosome subtomogram averages ex vivo” subsections and shortened the text as much as possible. The new subsection is entitled “Histone GFP-tagging and visualization ex vivo”

7) Page 16, Line 329. "Because all attempts to make H3- or H4-GFP "sole source" strains failed..." Is there a possible explanation here? Cytotoxic effect because of steric hindrance of nucleosomes?

Yes, it is possible that the GFP tag is interfering with the nucleosomes interactions with its numerous partners. It is also possible that the histone-GFP fusions do not import and/or assemble efficiently enough to support a bare-minimum number of functional nucleosomes. Given that the phenotypic consequences of fusion tags is an underexplored topic and that we don’t have any data on the (dead) transformants, we would prefer to leave out the speculation about the cause of death in the attempted creation of “sole source” strains.

Author Response

Reviewer #1 (Public Review):

The manuscript investigates how humans store temporal sequences of tones in working memory. The authors mainly focus on a theory named "Language of thought" (LoT). Here the structure of a stimulus sequence can be stored in a tree structure that integrates the dependencies of a stimulus stored in working memory. To investigate the LoT hypothesis, participants listened to multiple stimulus sequences that varied in complexity (e.g., alternating tones vs. nearly random sequence). Simultaneously, the authors collected fMRI or MEG data to investigate the neuronal correlates of LoT complexity in working memory. Critical analysis was based on a deviant tone that violated the stored sequence structure. Deviant detection behavior and a bracketing task allowed a behavioral analysis.

Results showed accurate bracketing and fast/correct responses when LoT complexity is low. fMRI data showed that LoT complexity correlated with the activation of 14 clusters. MEG data showed that LoT complexity correlated mainly with activation from 100-200 ms after stimulus onset. These and other analyses presented in the manuscript lead the authors to conclude that such tone sequences are represented in human memory using LoT in contrast to alternative representations that rely on distinct memory slot representations.

Strengths

The study provides a concise and easily accessible introduction. The task and stimuli are well described and allow a good understanding of what participants experience while their brain activation is recorded. Results are extensive as they include multiple behavioral investigations and brain activation data from two different measurement modalities. The presentation of the behavioral results is intuitive. The analysis provided a direct comparison of the LoT with an alternative model based on estimating a transition-probability measure of surprise.

For the fMRI data, the whole brain analysis was accompanied by detailed region of interest analyses, including time course analysis, for the activation clusters correlated with LoT complexity. In addition, the activation clusters have been set in relation (overlap and region of interest analyses) to a math and a language localizer. For the MEG data, the authors investigated the LoT complexity effect based on linear regression, including an analysis that also included transitional probabilities and multivariate decoding analysis. The discussion of the results focused on comparing the activation patterns of the task with the localizer tasks. Overall, the authors have provided considerable new data in multiple modalities on a well-designed experiment investigating how humans represent sequences in auditory working memory.

Weaknesses

The primary issue of the manuscript is the missing formal description of the LoT model and alternatives, inconsistencies in the model comparisons, and no clear argumentation that would allow the reader to understand the selection of the alternative model. Similar to a recent paper by similar authors (Planton et al., 2021 PLOS Computational Biology), an explicit model comparison analysis would allow a much stronger conclusion. Also, these analyses would provide a more extensive evidence base for the favored LoT model. Needed would be a clear argumentation for why the transitional probabilities were identified as the most optimal alternative model for a critical test. A clear description of the models (e.g., how many free parameters) and a description of the simulation procedure (e.g., are they trained, etc.) Here it would be strongly advised to provide the scripts that allow others to reproduce the simulations.

We thank the reviewer for the requests and critiques. Although this paper follows upon our extensive prior behavioral work (Planton et al.), we agree that it should stand alone and that therefore the models need to be described more fully. We have now added a formal description of the LoT in the subsection The Language of Thought for binary sequences in the Results section and have added a formal and verbal description of the selected sequences in Figure 1-figure supplement 1. Furthermore, we added a model comparison similar to the one done in (Planton et al., 2021 PLOS Computational Biology). This analysis is now included in Figure 2 and in the Behavioral data subsection of the Results section. It replicates previous behavioral results obtained in Planton et al., 2021 PLOS Computational Biology, namely that complexity, as measured by minimal description length in the binary version of the “language of geometry” was the best predictor of participants’ behaviour.

Interestingly, we found that the model that considered both complexity and surprise had even lower AIC suggesting that statistical learning is simultaneously occurring in the brain (Brain signatures of a multiscale process of sequence learning in humans, M Maheu, S Dehaene, F Meyniel - eLife, 2019). In this respect, we do not consider surprise from transition probabilities as an alternative model but rather as a mechanism that is occurring in parallel to sequence compression. The main goal of this work was to determine how sequence processing was affected by sequence structure, captured by the language of thought. In this line, we didn't select the tested sequences in order to investigate statistical learning but, instead, chose them with similar global statistical properties.

The MEG experiment provided us with the opportunity to separate temporally the contributions of statistical mechanisms from the ones of sequence compression according to the language of thought. Indeed, contrary to the fMRI experiment, we could model at the item level the statistical properties of individual sounds. We report the results when accounting jointly for statistical processing and LoT-complexity in Supplementary materials.

The different models considered in previous work didn’t need to be trained. The sequence complexity they provided could be analytically computed based on sequence minimal description length.

Furthermore, the manuscript needs a clear motivation for the type of sequences and some methodological decisions. Central here is the quadratic trend selectively used for the fMRI analysis but not for the other datasets.

To design the MEG, we had to decrease the number of sequences from 10 to 7. We selected them based on the LoT-complexity and the type of sequence information they spanned. As a consequence, the predictors for linear and quadratic complexity are very correlated (82%). Unfortunately, due to low SNR, this doesn’t allow to robustly account for the contributions of quadratic complexity in the MEG-recorded brain signals. Still, in response to the referee, we performed a linear regression as a function of quadratic complexity on the residuals of the regression as function of statistics and complexity that we report here. No significant clusters were found for habituation and standard trials but two were found (corresponding to the same topography) for deviant trials for late time-points.

In Author response image 1 regression coefficients for the quadratic complexity regressor regressed on the residuals of the surprise from transition probabilities and complexity. In Author response image 2, 2 significant clusters were found for the deviant sounds.

We also averaged the decoding scores from Figure7.A over the time-window obtained from the temporal cluster-based permutation test (see Author response image 2). The choice of complexity values didn’t allow any clear assessment of the contribution of the quadratic complexity term.

In summary, in the current design, we do not think that the number of tested sequences allows us to clearly conclude that no quadratic effect can be found for Habituation and Standard trials. We would need to re-design an experiment to test specifically the quadratic complexity contribution to brain signals in MEG.

Author response image 1.

Author response image 2.

Also, the description of the linear mixed models is missing (e.g., the random effect structure, e.g., see Bates, D., Kliegl, R., Vasishth, S., & Baayen, H. (2015). Parsimonious mixed models. arXiv preprint arXiv:1506.04967.). Moreover, sample sizes have not been justified by a power analysis.

The linear mixed model that is considered in this work is very simple, it only uses Subject as a random variable. This is now stated clearly in the corresponding part in the Experimental procedures section:

To test whether subject performance correlated with LoT complexity, we performed linear regressions on group-averaged data, as well linear mixed models including participant as the (only) random factor. The random effect structure of the mixed models was kept minimal, and did not include any random slopes, to avoid the convergence issues often encountered when attempting to fit more complex models.

Author Respoinse

Reviewer #2 (Public Review):

In the results of Fig. 2, the proteins are emitted at distance epsilon from the cortical boundary. From there, they locally perform 1D diffusion to the boundary, so most of them would readsorb once they diffuse a distance epsilon. Only a small fraction would extend past epsilon, which I assume is why the concentration drops by orders of magnitude beyond epsilon. Is such a concentration drop realistic given typical numbers of proteins in cells?

This is a good point. In [29], McInally et al. investigate kinesin-13 concentrations in Giardia and find that it drops sharply near the pole (about three to four orders of magnitude), as surmised by the referee. The drop off we see in our model is like what McInally et al see in terms of orders of magnitude decrease in the concentration gradient close to the pole.

It should be clarified if the proposed size scaling is independent of the specific choice of the distance epsilon of the point of protein release from the anterior pole. I don't see any reason why this distance should increase with cell size as epsilon = 0.05 R (on page with equation 5). It's unclear if the size scaling of the concentration gradient might be dependent on the assumption epsilon ~ R.

Figure R1 shows the dependence of the gradient on epsilon and see that the concentration gradient from the pole is unaffected everywhere beyond the source.

Figure R1. Concentration gradient for cells with the source at different distances from the pole (ϵ) Concentration profiles with differing source points. We start very close to the pole and move further away. The radius of the sphere is 10 μm, the diffusion constant D=1 μm^2/s and the transport speed along the cortex is v=1μm/s.

Author Response:

Reviewer #1 (Public Review):

This manuscript describes the role of PMd cck neurons in the invigoration of escape behavior (ie retreat from aversive stimuli located in a circumscribed area of the environment in which testing was conducted). Further, PMd cck neurons are shown to exert their effect on escape via the dorsal PAG. Finally, in an intriguing twist, aversive images are shown to increase the functional coupling between hypothalamus and PAG in the human brain.

The manuscript is broadly interdisciplinary, spanning multiple subfields of neuroscience research from slice physiology to human brain imaging.

We thank the Reviewer for recognizing the interdisciplinarity of our work.

To understand the novelty of the results obtained in the rodent studies, it is important to note that these data are a replication and elaboration of work published recently in Neuron by the primary authors of this manuscript. The current manuscript does not cite the Neuron paper.

We apologize for this omission. At the time of the current submission the Neuron paper had not been accepted and thus we could not cite it. We now discuss this paper in the introduction and highlight how the current manuscripts expand upon the data published in the Neuron paper.

The most novel aspect of the rodent experiments presented in this manuscript is the demonstration of a role for cck PMd neurons in invigorating behavioral withdrawal from cues associated with the kind of artificial stimuli commonly used in laboratory settings (ie a grid floor associated with shock). Unfortunately, these results are made somewhat difficult to interpret by a lack of counterbalancing - all subjects receive an assay of escape from a predator prior to the shock floor assay. Certainly, research on stress and sensitization tells us that prior experience with aversive stimuli can influence the response to aversive stimuli encountered in the future. Because the role of this pMD circuitry in predatory escape has already been demonstrated, this counterbalancing issues does somewhat diminish the impact of the most novel rodent data presented here.

Indeed, as the Reviewer states, prior exposure to aversive stimuli may influence responses to future exposures to threats. We opted to have the rat test before the shock grid test because the rat exposure is a milder experience than the shock grid test, as no actual pain occurs in the rat assay. We thus reasoned that the more intensely aversive assay (the shock assay) was more likely to influence behavior in the rat assay than vice-versa. Nevertheless, we agree with the Reviewer’s point that the lack of counterbalancing between the assays may mask potential influences of the rat assay on the shock grid assay behavior.

To address this issue we ran a cohort of new mice, showing that behavior in the shock grid assay is not affected by prior experience in the rat assay. We now show in Figure R1 and Figure 1, figure supplement 2 that freezing, threat avoidance and escape metrics in the shock grid assay are not significantly changed by prior exposure to the rat assay.

Figure R1. (Same as Figure 1, figure supplement 2). The order of threat exposure does not affect defensive behavior metrics. (A) Two cohorts of mice were exposed to the rat and shock grid threats in counterbalanced order, as specified in the yellow and green boxes. (B) The defensive behavioral metrics of these two cohorts were compared for the fear retrieval assay. None of the tested metrics were different between groups (Wilcoxon rank-sum test; each group, n=9 mice).

The manuscript concludes with an fMRI experiment in which the BOLD response to aversive images is reported to covary across the hypothalamus and PAG. It is intriguing that unpleasant pictures influence BOLD in regions that might be expected to contain circuits homologous to those demonstrated in rodents. It is important to note that viewing images is passive for the subjects of this experiment, and the data include no behavioral analogue of the escape responses that are the focus of the rest of the manuscript.

We agree with the Reviewer that there are many differences between the mouse and human behavioral tasks, and we have expanded the text highlighting these differences more clearly. One of our results, as highlighted by the Reviewer, is that inhibition of the PMd-dlPAG projection impairs escape from threats. Indeed, there is no escape in the human data, as stated by the Reviewer.

Now, we conducted new dual photometry recordings, in which we simultaneously monitor calcium transients in the PMd and the dlPAG in contralateral sides. Using these dual recordings, we show that mutual information between the PMd and the dlPAG in mice is higher during exposure to threats (rat and shock grid fear retrieval) than control assays (toy rat and pre-shock habituation) (Figure R2 and Figure 9 and Figure 9, figure supplement 1). Importantly, this analysis was also performed after excluding all time points that include escapes. Thus, the increase in PMd-dlPAG mutual information is independent of escapes, and is related to exposure to threats.

Similarly, the increase in activity in the human fMRI data in the hypothalamus-dlPAG pathway is also related to the exposure to aversive images, rather than specific defensive behaviors performed by the human subjects. This new finding of increased mutual information in the PMd-dlPAG circuit independently of escapes provides a better parallel to the human data.

In Figure R2 below we used mutual information instead of correlation because mutual information can capture both linear and non-linear correlation between two time-series. Figure R2E-G shows that the projection from PMd-cck cells to dlPAG is unilateral. Thus, in dual photometry recordings that were done contralaterally in the PMd and the dlPAG, the signals from the dlPAG are from local cell bodies, and are not contaminated by GCaMP signals from PMd-cck axon terminals.

Figure R2. (Panels from Figure 9(A-D) and from Figure 9, figure supplement 1 (panels E-G)) Dual fiber photometry signals from the PMd and dlPAG exhibit increased correlation and mutual information during threat exposure. (A) Scheme showing setup used to obtain dual fiber photometry recordings. (B) PMd-cck mice were injected with AAV9-Ef1a-DIO-GCaMP6s in the PMd and AAV9-syn-GCaMP6s in the dlPAG. (C) Expression of GCaMP6s in the PMd and dlPAG. (Scale bars: (left) 200 µm, (right) 150 µm) (D) Bars show the mutual information between the dual-recorded PMd and dlPAG signals, both including (left) and excluding (right) escape epochs, during exposure to threat and control. Mutual information is an information theory-derived metric reflecting the amount of information obtained for one variable by observing another variable. See Methods section for more details. (E) Cck-cre mice were injected with AAV9-Ef1a-DIO-YFP in the PMd in the left side. (F) Image shows the expression of YFP in PMd-cck cells in the left side. (scale bar: 200 µm) (G) PMd-cck axon terminals unilaterally express YFP in the dlPAG. (scale bar: 150µm). * p<0.05, ** p<0.01.

Reviewer #2 (Public Review):

The manuscript by Wang et al. addresses neuronal mechanisms underlying conserved escape behaviors. The study targets the midbrain periaqueductal grey, specifically the dorsolateral aspect (dlPAG), since previous research demonstrated that activation of dlPAG leads to escape behaviors in rodents and panic-related symptoms in humans. The hypothalamic dorsal premammillary nucleus (PMd) monosynaptically projects to the dlPAG and thus could play a role in escape behavior. The authors test whether cholecystokinin (CCK)-expressing PMd cells could be involved in escape behaviors from innate and conditioned threats using mainly two behavioral paradigms in mice: exposure to a live rat and electrical foot shocks.

Different approaches are used to test the main hypothesis. Using fiber photometry and microendoscopy calcium imaging in freely moving mice, the study finds that PMd CCK+ neurons were more active when mice are close to threats and during escape behaviors. Furthermore, PMD CCK+ activation patterns predicted escape behavior in a general linearized model. Chemogenetic inhibition of CCK+ PMd cells decreased escape speed from threats in both behavioral paradigms, while optogenetic activation of those cells lead to an increase in speed. Observation of c-fos expression after optogenetic activation revealed activation within two target areas of the PMd, the dlPAG and anteromedial ventral thalamus (AMv), in which cellular activity measured by fiber photometry also increased during escape behaviors. Interestingly, inhibition of PMd-to-dlPAG pathway, but not PMd-to-AMv, caused a decrease in escape velocity. Lastly, the authors investigated the response of several human participants to threatening images in an fMRI scan. These results suggest that similar to mice, an activation proportional to the threat intensity within a functional connection between hypothalamus and PAG pathway may occur in humans.

The authors conclude that a pathway from the PMd to the dlPAG, characterized by expression of CCK, control escape vigor and responsiveness to threat in mice, and that a similar pathway could be present in humans.

Overall, the comprehensive data from multiple approaches support a role of the identified pathway in escape behavior. However, an insufficient description of the used methods and experimental details makes it difficult to assess the validity and conclusivity of some findings. In addition, the strong interpretation emphasis on the functional specificity of the CCK+ PMd-dlPAG pathway appears not fully supported by the data.

1) The rationale for selection of CCK+ cells of the PMd is missing in the current manuscript. Despite methodological considerations, a clear description of these cells' role and characteristics from the existing literature is needed.

To address this point, we justify our choice of cck+ cells by discussing prior data showing that PMd cck cells are the major neuronal population of the PMd. Furthermore, cck is not strongly expressed in other adjacent hypothalamic nuclei, showing the high anatomical specificity of our manipulations targeting PMd-cck cells. We also discuss prior data (Wang et al., 2021) in the Introduction and Discussion about these cells.

2) The narrowness of the conclusions of the article is unnecessary. Although CCK+ PMd cells could play a role in regulating escape vigor, some of the presented results rather support the notion of a more general role of these cells in mediating defensive states. For example, the photometry data shows correlation of activity with other active defensive behavior. To address this point, a better analysis of the relation between neuronal activity and the general locomotor behavior of the animals is lacking. In addition, the already presented relation with the measured behaviors is not taken into account when interpreting the results (e.g. Fig 7 E). This description would be relevant to more comprehensively attributing functional roles for CCK + PMd cells.

At the Reviewer's request, we have included an analysis of the relationship between general locomotor behavior and PMd-cck df/F (Figure R3 and Figure 2, figure supplement 2). Interestingly, we found that the df/F increases monotonically with increasing ranges of speed and acceleration in the threat assays, while remaining fairly constant for matched ranges in the control assays.

We agree with the Reviewer that Figure 7E shows PMd-cck cells are activated not only during escape, but also other behaviors. However, the chemogenetic inhibition data show that PMd-cck cell activity only impaired escape speed, without altering freezing, approach or stretch-attend postures. Thus, the chemogenetic inhibition data indicates that the activity of these cells is only critical for escape, among the behaviors scored. Nevertheless, we discussed a “notion of a more general role of these cells in mediating defensive states” as suggested by Reviewer 2. However, Reviewer 1 provided the opposite feedback, stating that “It needs to be made clear that a specific role of PMd in quantitative measures of escape is the new result, instead of a broader role for this region”. Considering these opposing suggestions, we broadened the discussion on the role of the PMd, but did so conservatively.

Figure R3. (Same as Figure 2, figure supplement 2). Bars show the mean PMd-cck df/F (z-scored) for increasing ranges of (A) speed and (B) acceleration. (Wilcoxon signed-rank test; n=15) * p<0.05, ** p<0.01, *** p<0.001.

3) The imprecision of the methods description, especially the behavioral analysis is contributing to the previous point. In particular, the escape criterion itself seems to include a vague classification based on movement away from the threat- this should be more concretely defined (e.g. using angle of escape direction). In any case, the different behavioral context dimensions between the two paradigms would probably affect the escape criterion itself and thus have to be taken into account when interpreting the results.

The Reviewer makes an important point that the escape definition included in the Methods section was lacking in detail, specifying only a minimum directional speed. We had neglected to include two crucial criteria that were used as well: a minimum distance-from-threat at which escape must be initiated and a minimum distance traversed during escape. All escapes were therefore required to begin near the threat and lead to a substantial increase in mouse distance from the threat. These details are now included in the Methods section, as follows:

“'Escapes' were defined as epochs for which (1) the mouse speed away from the threat or control stimuli exceeded 2 cm/s for a minimum of 5 seconds continuously, (2) movement away from the threat was initiated at a maximum distance-from-threat of 30 cm and (3) the distance traversed from escape onset to offset was greater than 10 cm. Thus, escapes were required to begin near the threat and lead to a quick and substantial increase in distance from the threat.

'Escape duration' was defined as the amount of time that elapsed from escape onset to escape offset.

'Escape speed' was defined as the average speed from escape onset to offset.

'Escape angle' was defined as the cosine of the mouse head direction in radians, such that the values ranged from -1 (facing towards the threat) to 1 (facing away from the threat). Mouse head direction was determined by the angle of the line connecting a point midway between the ears and the nose.”

Using the escape definition above, a higher number of escapes and a higher average escape speed was observed in threat assays compared to control assays (Figure 1). This finding indicates that the definitions we used are capturing defensive evasion.

Both contexts have a length of 70 cm, so differences in the length of the contexts did not influence the definition of escape across contexts.

In response to the Reviewer's suggestion of an escape angle criterion, we have included Figure R4 which illustrates that, using the aforementioned escape definition, the resulting escape angle is quite stereotyped. The cosine of the escape angle shows very little variation, showing that only a narrow range of escape angles is used. Given this result, we opted to not include the angle of escape as part of the escape criteria to increase simplicity.

Figure R4. (A) Lines represent mouse position for all escapes that occurred during an example rat (top) and fear retrieval (bottom) session. Note that, while there is a diversity of escape routes, the escape angle is quite similar. (B) (left) Diagram provides a description of the escape angle metric, here calculated as the cosine of the head direction in radians. A value of 1 indicates an escape parallel with the long walls of the enclosure. (right) Bars represent the mean escape angle for all animals in Figure 1 during the rat and fear retrieval assays (n=32). As is apparent in (A), the mean escape angle cosine has little variability.

4) In line, more detailed descriptions of the animal's behavior are needed to support assessment of the results regarding the event-related fiber photometry results. Measures like frequency of escape, duration of freezing bouts and angle, duration and total speed of the escape bouts, and a better description of measures like Δ escape speed could be relevant for interpreting the results. In addition, there is no explanation of how the possible overlapping of behaviors in the broad time frame used in the experiments was regarded.

We have now included the requested measures as a supplement to Figure 2 (see also Fig. R5 below). Regarding overlapping behaviors, we have quantified the overlap between categorized behaviors in the fiber photometry assay and found that only a small fraction of behavioral timepoints were categorized as more than one behavior, primarily during behavioral transitions. This is quantified in Figure R6 below. Moreover, as is now described in the Methods, the analyses presented in Figure 2G-I (as well as Figure 7C-E, 7G-I) were performed only on behaviors that were separated from all other behaviors by a minimum of 5 seconds.

Figure R5. (Same as Figure 2, figure supplement 1) Behavioral metrics for the PMd fiber photometry cohort during threat exposure assays. (A) Diagram provides a description of the escape angle metric, here calculated as the cosine of the head direction in radians. A value of 1 indicates an escape parallel with the long walls of the enclosure. (B) Table shows pertinent defensive metrics during exposure to rat and fear retrieval assays for the PMd fiber photometry cohort. (n=15 mice).

Figure R6. The behavioral overlap between classified behaviors is minimal. The colormap depicts the fraction of behavioral timepoints for each of the four classified behaviors that was categorized as each of the remaining behaviors across all PMd fiber photometry assays (n=15 mice).

5) Part of the experimental results provide suboptimal evidence for the provided interpretation. That is, the lack of clear quantification and statistical analysis of the microendoscopy calcium imaging data on PMd-CCK+ cells makes it hard to reconcile this data with the photometry data. Furthermore, evidence through c-Fos staining after optogenetically stimulation of PMd-cck+ cells is insufficient evidence for the interpretation of broad, but functionally specific, recruitment of defensive networks. While the data on optogenetic inhibition of the PMd-CCK+ projection to the dlPAG seems to confirm the main hypothesis, both an intra-animal control and demonstration of statistical significance in the analysis are desirable to fully support that role.

We agree with the Reviewer that clear quantification and statistical analyses are essential in interpreting the microendoscopic analysis. However, we are not sure what is being requested, as we have applied both of these approaches to this dataset. For instance, in Figure 3, we quantify the percentage of cells that significantly encode each behavior as well as implement 5-fold logistic regression to determine how well these behaviors can be predicted. This accuracy is statistically compared to chance. Further quantification and statistical comparisons of speed and position decoding accuracy between threat and control assays are included in Figure 4. Concerning the Arch experiments, we have included an intra-animal control by comparing light off and on epochs, and we statistically compare the difference between these epochs with a control group.

Regarding the c-Fos experiment, we observe increased cfos expression in several nuclei known to be critical for defense, such as the bed nucleus of the stria terminalis and the ventromedial hypothalamus. This finding underlies our claim that optogenetic activation of the PMd recruits defensive networks. Nevertheless, it is entirely possible that naturalistic endogenous activation of the PMd does not recruit these nuclei. We added text addressing this caveat.

6) The provided fMRI data only provides circumstantial evidence to support a functionally specific hypothalamus to PAG pathway especially due to the technical characteristics and limitations of the experimental setup and behavioral paradigm.

The Reviewer makes an excellent point. Please see our response to Reviewer 1, point 6, where we provide a better parallel to the fMRI data in a new photometry analysis, as well as the added Figure 9.

Briefly, we now have conducted contralateral dual photometry recordings of the dlPAG and the PMd, and show an increase in mutual information between the neural activity of these two regions during exposure to threats. This result was found after removing all timepoints with escapes. Thus, the increase in mutual information is related broadly to threat exposure, rather than caused by specific moments during which escape occurs. We argue that this result more closely parallels the human data, as both the fMRI and mutual information from mice data show an increase in functional connectivity in the hypothalamus-dlPAG pathway during threat exposure, independently of escapes.

Reviewer #3 (Public Review):

This manuscript by Wang et al extends the Adhikari lab's earlier findings of the hypothalamic dorsal premammillary nucleus' role in defensive behavior. Using cell-type specific calcium imaging, the authors show that the activity of CCK-expressing PMd neurons precedes and predicts escape from both learned and unlearned threats. Optogenetic/chemogenetic inhibition revealed that the PMd-dlPAG pathway contributes to escape vigor. Additionally, optogenetic activation of CCK PMd neurons induces Fos in numerous brain regions implicated in fear and escape behaviors. Last, an analogous hypothalamic-PAG pathway in humans is shown to be activated by aversive images in humans.

Although these findings are potentially impactful, additional clarification and data are needed to strengthen and streamline the manuscript, as outlined below.

1) The results of the authors' recent publications (Wang et al Neuron 2021, Reis et al J. Neuro 2021) should be integrated into the manuscript. For example, the rationale for selectively manipulating CCK+ PMd neurons is not stated. Likewise, histological validation that the Cre-dependent GCaMP expression is restricted to CCK+ neurons should be shown or referenced. The authors should also provide discussion as to how the current results integrate with their other recent findings.

Following the Reviewer’s suggestions, we address these concerns by referencing our previous paper. Cck+ cells were chosen because this marker is expressed in over 90% of PMd cells (Wang et al., 2021), but not in adjacent nuclei (Mickelsen et al., 2020). These cells have also been shown to be important to control escape from innate threats, such as carbon dioxide (Wang et al., 2021). These are the justifications for selecting PMd-cck cells, as discussed in this revised submission. We also reference our prior work to indicate specific expression of GCaMP in PMd cck cells.

2) The authors used male and female mice in their experiments but there are no analyses of potential sex differences in threat responses or escape vigor. Were there any significant sex differences in the measurements presented in Figure 1? A supplementary figure showing data for male and female mice would be helpful. Also, for Figure 1, please display the individual data points so that the reader can appreciate the variability in the behavioral responses. How many approaches and escapes are observed in each test? What is the average duration of a freezing bout?

As the results reported in Figure 1 summarize data from a rather large cohort (n=32), we decided it best for clarity's sake to show the variability in behavioral responses as a histogram of the difference scores for each animal (threat - control), now included as Figure 1, Figure Supplement 1, as well as below (Figure R7). Showing 32 individual data points may make the figure difficult to visualize (but of course, we can instead plot these individual points if the Reviewer prefers that instead of the plots shown below). At the Reviewer's request, we have also included the number of approaches and escapes in Figure 1 and the supplement. The average duration of a freezing bout is 2.03s ± 0.15 and is now reported in the Results section. There were no significant sex differences in the Figure 1 measures, and this is stated in the text, as well as plotted below in Figure R8 (male n=17, female n=15; Wilcoxon rank-sum test, p>0.05).

Figure R7. (Also Figure 1, figure supplement 1) Distribution of the difference scores for threat - control assays. Histograms depict the difference scores for all mice, threat - control, for each behavioral metric in Figure 1. The dotted red line indicates zero, or no difference between threat and control (n=32 mice).

Figure R8 (Also Figure 1, Figure supplement 3). Distribution of the difference scores for threat - control assays for males and females. Histograms depict the difference scores for all mice, threat - control, for each behavioral metric in Figure 1, separately for males (green) and females (purple). The dotted red line indicates zero, or no difference between threat and control (male n=17, female n=15). No significant differences (p>0.05) were found between males and females in any of the metrics plotted.

3) In Fig. 2, there appears to be sustained activity of CCK+ neurons after the onset of threat approach, and ramping activity preceding stretch-attend. In-depth analysis of these responses may be beyond the scope of this study, but the findings should be discussed since the representation of approach-related behaviors indicates the PMd is involved in more general representation of threat proximity, rather than simply escape vigor.

We agree with the Reviewer that PMd-activity represents distance to both innate and conditioned threats. We also include new data showing that PMd-dlPAG mutual information increases in the presence of threats (Figure R2 and Figure 9). Taken together, these data show that PMd activity encodes more than just escape vigor. We have altered the text to emphasize these results. These dual-site recordings were done contralaterally, so that dlPAG-syn cell body GCaMP signals are not contaminated by GCaMP-expressing PMd-cck axon terminals in the dlPAG.

4) The authors state that PMd CCK neuronal activity regulates escape vigor. Although the authors show a correlation of the calcium signal amplitude and escape distance in Fig. 2I, a correlation with escape velocity would be a more convincing measure of vigor.

PMd-cck neural activity is related to escape speed, as shown by single cell miniaturized microscopy recordings. Figure 4D shows that PMd ensemble activity can predict escape speed from threats, but not control stimuli. These results were specific to escape, as PMd activity did not encode approach speed towards threats or control stimuli (Figure 4D). Furthermore, we performed new analysis and showed that a greater number of PMd cells show activity significantly correlated with escape from threats, compared to control stimuli. Finally, we have additionally shown that, for the cells whose activity is significantly correlated with escape speed, the mutual information between escape speed and df/F is significantly greater for threat than control. This has now been included as Figure 3I-K (same as Figure R9 below).

Figure R9. A higher fraction of PMd-cck cells are correlated with escape speed during exposure to threats. (Also Figure 3I-J) (A) Traces show the z-scored df/F (blue) and speed (gray) for one cell classified as a speed cell in the rat exposure assay (top) and one non-correlated cell from the toy rat assay (bottom). Individual escape epochs are indicated by red boxes. (B) Bars show the percent of cells that significantly correlate with escape speed. (Fisher's exact test; toy rat: n correlated = 56, n non-correlated = 405; rat: n correlated = 100, n non-correlated = 366; pre-shock: n correlated = 50, n non-correlated = 571; fear retrieval: n correlated = 122, n non-correlated = 391) (C) Bars show the mutual information in bits between escape speed and calcium activity for cells whose signals were significantly correlated with escape speed in (J). (Wilcoxon rank sum test; toy rat n=56, rat n=100; pre-shock n=50, fear retrieval n=122). p<0.001.

Unfortunately, the lower resolution provided by photometry did not reveal consistent correlations with escape velocity across assays. Despite this lack of single cell resolution, PMd-cck photometry amplitude correlated with escape velocity during exposure to the rat, but not the toy rat, as shown below (Figure R10). However, this result was not replicated in the fear retrieval assay. Taken together, these data show that PMd activity is indeed related to escape vigor.

Figure R10. Escape speed correlates with PMd-cck photometry amplitude during rat exposure. Bars depict the Spearman r-value of escape speed and PMd-cck photometry df/F (z-scored) amplitude during exposure to rat and toy rat. (n=9 mice) p<0.001.

5) The changes in prediction error from control to threat contexts in Figs. 4B and 4D are compelling, but the prediction error in the threat context seems high. Can the authors provide a basis for what constitutes a 'good' error score?

We have now included the chance error, calculated by training and testing the GLM on circularly permuted data across mice and indicated below with a dotted red line in Figure 4 and its supplement. The Methods have also been updated to reflect this new aspect of the analysis. A ‘good’ error would be a value that is significantly lower than the error expected by chance, which is indicated by the red dashed line in Figure R11.

Fig. R11. (Also Figure 4B, 4D and Figure 4, figure supplement 1) (A) Bars show the mean squared error (MSE) of the GLM-predicted location from the actual location. The MSE is significantly lower for threat than control assays (Wilcoxon signed-rank test; n=9 mice). The dotted red line indicates chance error, calculated by training and testing the GLM on circularly permuted data. Only threat assay error was significantly lower than chance (Wilcoxon signed-rank test; rat p<0.001, fear retrieval p=0.003). (B) Bars depict the MSE of the GLM-predicted velocity away from (left) and towards (right) the threat. The GLM more accurately decodes threat than control velocities for samples in which the mice move away from the threat (top). Only threat assay error was significantly lower than chance (Wilcoxon signed-rank test; rat p=0.004, fear retrieval p=0.012). (C) Bars depict the mean squared error of the GLM-predicted speed. The GLM more accurately decodes threat than control speeds. Only threat assay error was significantly lower than chance (rat p<0.020, fear retrieval p=0.040). (Wilcoxon signed-rank test; n=9 mice) p<0.01.

6) Off-target effects are a potential concern at the dose of CNO used (5 mg/kg). For example, the increased approach speed with CNO in the YFP control group (Fig. 5D) may be a result of the high CNO dose. How was the dose of CNO selected?

This dose was selected based on our prior experience using the same dose to study PMd-cck cells in our prior Neuron paper. Additionally, this is a common dose, used in many papers. Indeed, there are several recent neuroscience papers published in this journal, eLife, that use this exact dose of CNO (Chen et al., 2016; Halbout et al., 2019; Ito et al., 2020; Kwak and Jung, 2019; Li et al., 2020; Mukherjee et al., 2021; O’Hare et al., 2017; Patel et al., 2019).

Although in this particular case approach velocity trended higher after CNO treatment, this is not a consistent result. We ran another cohort of control mice (n=9 saline, 9 CNO 5 mg/kg) and show that no such trend in approach velocity to the shock grid was observed during fear retrieval (Figure R12).

Fig. R12. CNO has no effect on approach velocity in a separate control cohort. The experimental protocol was performed as described in Figure 1B for a control cohort. For this group, CNO injection had no significant effect on approach speed (Wilcoxon signed-rank test, n=9).

7) Given the visible trends in the data, the number of animals used in Fig. 6B is insufficient to make conclusions about the behavioral effect of optogenetic excitation of PMd CCK neurons. Either more animals should be added, or the analysis should be limited to the Fos staining.

At the Reviewer's request, we have increased the number of animals in this analysis and found the results unchanged. Figure 6B has been replaced in the main manuscript (same as Figure R13 below). The addition of these new animals also erased the previous non-significant trends seen with fewer animals.

Figure R13. (Also Figure 6B) Delivery of blue light increases speed in PMd-cck ChR2 mice, but not stretch-attend postures or freeze bouts. (PMd-cck YFP n=6, PMd-cck ChR2 n=8; Wilcoxon rank-sum test).

Author Response

Reviewer #1 (Public Review):

The actual description of the methods does not allow the reader to evaluate the precision of two important processing steps. First, rCBF measures are supposed to be restricted to the cortex, but given the pCASL image spatial resolution, partial volume effects with white matter probably exist, especially in younger infants. Furthermore, segmenting tissues on the basis of anatomical images (especially T1-weighted) is complicated in the first postnatal year. As rCBF measurements are very different between grey and white matter, the performed procedure might impact the measures at each age, or even lead to a systematic bias on age-dependent changes. Second, the methodology and accuracy of the brain registration across infants are little detailed whereas it is a challenging aspect given the intense brain growth and folding, the changing contrast in T1w images at these ages, and the importance of this step to perform reliable voxelwise comparison across ages.

We thank the reviewer for this comment. We have added more descriptions in the methods to address this comment. Briefly, individual rCBF map was generated in the individual space and calibrated by phase contrast MRI to minimize the individual variations of processing parameters such as T1 of arterial blood (Aslan et al., 2010). Cortical segmentation was also conducted in individual space. Then different types of images including rCBF map and gray matter segmentation probability map in the individual space were normalized into the template space. An averaged gray matter probability map was generated after inter-subject normalization. After carefully testing multiple thresholds in the averaged gray matter probability maps, 40% probability minimizing the contamination of white matter and CSF while keeping the continuity of the cortical gray matter mask across the cerebral cortex was used to generate the binary gray matter mask shown on the left panel of Figure R1 below. Despite poor contrasts and poor cortical segmentation of T1-weighted images of younger infants rightfully pointed out by this reviewer, the poor cortical segmentation of younger infants was compensated by the averaged cortical mask and measurement of rCBF in the template space. As demonstrated in the right three panels in Figure R1, the rCBF measure in the cortical mask in the template space is consistent across ages for accurate and reliable voxelwise comparison across age.

Figure R1. The gray matter mask and segmented cortical mask overlaid on rCBF map of three representative infants aged 3, 6, and 20 months in the template space. The gray matter mask on the left panel was created to minimize the contamination of white matter and CSF while keeping the continuity of the cortical gray matter mask across the cerebral cortex. The contour of the gray matter mask was highlighted with bule line.

The authors achieved their aim in showing that the rCBF increase differs across brain regions (the DMN showing intense changes compared to the visual and sensorimotor networks). Nevertheless, an analysis of covariance (instead of an ANOVA) including the infants' age as covariate (in addition to the brain region) would have allowed them to evaluate the interaction between age and region (i.e. different slopes of age-related changes across regions) in a more rigorous manner. Regarding the evaluation of the coupling between physiological (rCBF) and functional connectivity measures, the results only partly support the authors' conclusion. Actually, both measures strongly depend on the infants' age, as the authors highlight in the first parts of the study. Thus, considering this common age dependency would be required to show that the physiological and connectivity measurements are specifically related and that there is indeed a coupling.

We thank the reviewer for this comment. Following the reviewer’s suggestion, we conducted an analysis of covariance (ANCOVA) and found significant interaction between regions and age (F(6, 322) = 2.45, p < 0.05) with age as a covariate. This ANCOVA result is consistent with Figure 3c showing differential rCBF increase rates across brain regions. The ANCOVA result was added in the last paragraph in the Results section “Faster rCBF increases in the DMN hub regions during infant brain development”.

Regarding the evaluation of the coupling between physiological (rCBF) and functional connectivity measures (FC), the Figure 5, Figure 5–figure supplement 1 and 2 were generated exactly to test that the FC-rCBF coupling specifically localized in the DMN is not due to mutual age dependency. Briefly, Figure 5B demonstrated significant correlation only clustered in the DMN regions using the correlation method demonstrated in Figure 5-figure supplement 1. Furthermore, nonparametric permutation tests with 10,000 permutations were conducted. Such permutation tests are sensitive and effective with Figure 5c revealing significant coupling only in the DMN regions. If coupling is related to mutual age dependency, Figure 5c would demonstrate significant coupling in Vis and SM network regions too.

Author Response:

Reviewer #2:

In Zhang et al.'s paper, with 7T fMRI, they used different face parts as stimuli to explore the functional organization within the face specific areas, and found consistent patterns between different subjects in rFFA and rOFA. In these areas, the posterior region was biased to eye, and the anterior region was biased to mouth. To exclude potential confounds, they also ran several control experiments to show that the preference to eyes and mouth is not due to the eccentricity or upper-lower visual field preference. Based on what they found, they claim that there exists a finer scale functional organization within the face areas.

In general, I think the whole study is carefully designed, and the results are solid and interesting. However, I am not very comfortable about the claim about the organization of the face areas. Typically, when we talk about the organization, it either has more than 2 subdivisions or it has a continuous representation of certain features. In this paper, the results are mainly about the comparison between two face parts, and they failed to find other distinctive subareas showing preference to other face parts. Therefore, I would suggest that the authors could tune down their claim from functional organization to functional preference.

We have followed the advice from the reviewer to tune down the claim of functional organization in our manuscript. To emphasize both the functional preferences to different face parts within face-selective regions and the consistent spatial profile across different individuals, we now use “spatial tuning of face parts” in the manuscript.

Reviewer #3:

Zhang and colleagues investigated the spatial distribution of feature tuning for different face-parts within face-selective regions of human visual cortex using ultra-high resolution 7.0 T fMRI. By comparing the response patterns elicited by images of face-parts (hair, eyes, nose, mouth and chin) with whole faces, they report a spatial pattern of tuning for eyes and mouth along the posterior-anterior axis of both the pFFA and OFA. Within the pFFA this pattern spatial tuning appeared to track the orientation of the mid fusiform sulcus - an anatomical landmark for face-processing in ventral temporal cortex. Two additional control experiments are conducted to examine the robustness of the original findings and to rule out potentially confounding variables. These data are consistent with recent evidence for similar face-part tuning in the OFA and add to the growing body of work showing the topographical mapping feature based tuning within visual cortex.

The conclusions of this paper are mostly supported by the data, but some aspects of the data acquisition, analysis and interpretation that require further clarification/consideration.

1) It is currently unclear whether the current data are in full agreement with recent work (de Haas et al., 2021) showing similar face-part tuning within the OFA (or IOG) bilaterally. The current data suggest that feature tuning for eye and mouth parts progresses along the posterior-anterior axis within the right pFFA and right OFA. In this regard, the data are consistent. But de Haas and colleagues also demonstrated tuning for visual space that was spatially correlated (i.e. upper visual field representations overlapped upper face-part preferences and vice-versa). The current manuscript found little evidence for this correspondence within pFFA but does not report the data for OFA. For completeness this should be reported and any discrepancies with either the prior, or between OFA and pFFA discussed.

In the current study, three participants had data from both retinotopic mapping and face part mapping experiments. Consistent and robust part clustering were found in the right pFFA and right OFA. Following the reviewer’s suggestion, we analyzed these data for the right OFA and found the spatial patterns of eyes vs. mouths are similar to the patterns of visual field sensitivity on the vertical direction (i.e., upper to lower visual field), which are consistent with de Haas and colleagues’ findings. Note that we used more precise functional localization of OFA, while de Haas et al’s analysis was based on anatomically defined IOG, for which OFA is a part of. We have added this result in the Results session (Page 16), and also added a supplemental Figure 4-figure supplement 1.

2) It is somewhat challenging to fully interpret the responses to face-parts when they were presented at fixation and not in the typical visual field locations during real-world perception. For instance, we typically fixate faces either on or just below the eyes (Peterson et al., 2012) and so in the current experiment the eyes are in the typical viewing position, but the remainder of the face-parts are not (e.g. when fixating the eyes, the nose mouth and chin all fall in the lower visual field but in the current experimental paradigm they appear at fixation). Consideration of whether the reported face-part tuning would hold (or even be enhanced) if face-parts were presented in their typical locations should be included.

Our early visual cortex and some of the object-selective visual areas are sensitive to visual field locations. To dissociate the visual field tuning and face part tuning in face processing regions, in the main experiment of the current study the face part stimuli were presented at fixation to avoid the potential confounding contribution from visual field location. The spatial correlation between face part tuning and visual field tuning has been observed in posterior part of the face network. It is unlikely that presenting the face parts at the fixation was responsible for the observed face part tuning. To directly test the role of stimulus location, we reanalyzed the data from control experiment 2 in which face parts were presented at their typical locations. Contrasting eyes above fixation vs. nose & mouth below fixation revealed similar anterior-posterior bias in the right pFFA, showing that the face part tuning in the right pFFA is invariant to the visual field location of stimuli. See comparison in the figure below, note that the maps of eyes on top vs. nose & mouth on bottom are unsmoothed:

3) Although several experiments (including two controls) have been conducted, each one runs the risk of being underpowered (n ranges 3-10). One way to add reassurance when sample sizes are small is to include analyses of the reliability and replicability of the data within subjects through a split-half, or other cross-validation procedure. The main experiment here consisted of eight functional runs, which is more than sufficient for these types of analyses to be performed.

Following the reviewer’s suggestion, we split the eight runs data from each participant in the main experiment into two data sets (odd-runs and even-runs), and estimated the eyes-mouth biases within each data set. Then we calculated the correlation coefficient between such biases across different voxels between the two data sets to estimate the reliability of the results in the right pFFA. The results demonstrate strong reliability of the data within participants. We have added these results in the Results session (Page 7 and Figure 2-figure supplement 1).

4) The current findings were only present within the right pFFA and right OFA. Although right lateralisation of face-processing is mentioned in the discussion, this is only cursory. A more expansive discussion of what such a face-part tuning might mean for our understanding of face-processing is warranted, particularly given that the recent work by de Haas and colleagues was bilateral.

The right lateralization of face-processing has been observed in face-selective network. Both the neural selectivity to faces (Kanwisher et al., 1997) and the decodable neural information of faces (Zhang et al., 2015) are higher in the right than in the left hemisphere. The neural clustering of face part tuning and consistent spatial patterns across individuals in the right rather than in the left face selective regions provides a potential computational advantage for right lateralization for face processing. The clustering of neurons with similar feature tuning have been found extensively in the ventral pathway, which may help to support a more efficient neural processing. Therefore, one of the neural mechanisms underlying the functional lateralization of face processing could be the existence of spatial clustering of face part tunings in the right hemisphere. We have added more discussion about the relevance between our results and lateralization of face processing.

Author Response

Reviewer #1 (Public Review):

Briggs et al use a combination of mathematical modelling and experimental validation to tease apart the contributions of metabolic and electronic coupling to the pancreatic beta cell functional network. A number of recent studies have shown the existence of functional beta cell subpopulations, some of which are difficult to fully reconcile with established electrophysiological theory. More generally, the contribution of beta cell heterogeneity (metabolism, differentiation, proliferation, activity) to islet function cannot be explained by existing combined metabolic/electrical oscillator models. The present studies are thus timely in modelling the islet electrical (structural) and functional networks. Importantly, the authors show that metabolic coupling primarily drives the islet functional network, giving rise to beta cell subpopulations. The studies, however, do not diminish the critical role of electrical coupling in dictating glucose responsiveness, network extent as well as longer-range synchronization. As such, the studies show that islet structural and functional networks both act to drive islet activity, and that conclusions on the islet structural network should not be made using measures of the functional network (and vice versa).

Strengths:

• State-of-the-art multi-parameter modelling encompassing electrical and metabolic components.

• Experimental validation using advanced FRAP imaging techniques, as well as Ca2+ data from relevant gap junction KO animals.

• Well-balanced arguments that frame metabolic and electrical coupling as essential contributors to islet function.

• Likely to change how the field models functional connectivity and beta cell heterogeneity.

Weaknesses:

• Limitations of FRAP and electrophysiological gap junction measures not considered.

• Limitations of Cx36 (gap junction) KO animals not considered.

• Accuracy of citations should be improved in a few cases.

We thank reviewer 1 for their positive comments, including the many strengths in the approaches, arguments and impact. We do note the weaknesses raised by the reviewer and have addressed them following the comments below.

We would like to also note that when we refer to metabolic activity driving the functional network, we are not referring to metabolic coupling between beta cells. Rather we mean that two cells that show either high levels of metabolic activity (glycolytic flux) or that show similar levels metabolic activity will show increased synchronization and thus a functional network edge as compares to cells with elevated gap junction conductance. Increased metabolic activity would likely generate increased depolarizing currents that will provide an increased coupling current to drive synchronization; whereas similar metabolic activity would mean a given coupling current could more readily drive synchronized activity. We have substantially rewritten the manuscript to clarify this point.

Reviewer #2 (Public Review):

In their present work, Briggs et al. combine biophysical simulations and experimental recordings of beta cell activity with analyses of functional network parameters to determine the role played by gap-junctional coupling, metabolism, and KATP conductance in defining the functional roles that the cells play in the functional networks, assess the structure-function relationship, and to resolve an important current open question in the field on the role of so-called hub cells in islets of Langerhans.

Combining differential equation-based simulations on 1000 coupled cells with demanding calcium, NAPDH, and FRAP imaging, as well as with advanced network analyses, and then comparing the network metrics with simulated and experimentally determined properties is an achievement in its own right and a major methodological strength. The findings have the potential to help resolve the issue of the importance of hub cells in beta cell networks, and the methodological pipeline and data may prove invaluable for other researchers in the community.

However, methodologically functional networks may be based on different types of calcium oscillations present in beta cells, i.e., fast oscillations produced by bursts of electrical activity, slow oscillations produced by metabolic/glycolytic oscillations, or a mixture of both. At present, the authors base the network analyses on fast oscillations only in the case of simulated traces and on a mixture of fast and slow oscillations in the case of experimental traces. Since different networks may depend on the studied beta cell properties to a different extent (e.g., fast oscillation-based networks may, more importantly, depend on electrical properties and slow oscillationbased networks may more strongly depend on metabolic properties), it is important that in drawing the conclusions the authors separately address the influence of a cell's electrical and metabolic properties on its functional role in the network based on fast oscillations, slow oscillations, or a mixture of both.

We thank reviewer 2 for their positive comments, including addressing the importance of this study as it pertains to islet biology and acknowledging methodological complexities of this study. We also thank the reviewer for their careful reading and providing useful comments. We have integrated each comment into the manuscript. Most importantly, we have now extended our analysis to both fast and slow oscillations by incorporating an additional mathematical model of coupled slow oscillations and performing additional experimental analysis of fast, slow, and mixed oscillations.

Reviewer #3 (Public Review):

Over the past decade, novel approaches to understanding beta cell connectivity and how that contributes to the overall function of the pancreatic islet have emerged. The application of network theory to beta cell connectivity has been an extremely useful tool to understand functional hierarchies amongst beta cells within an islet. This helps to provide functional relevance to observations from structural and gene expression data that beta cells are not all identical.

There are a number of "controversies" in this field that have arisen from the mathematical and subsequent experimental identification of beta "hub" cells. These are small populations of beta cells that are very highly connected to other beta cells, as assessed by applying correlation statistics to individual beta cell calcium traces across the islet.

In this paper Briggs et al set out to answer the following areas of debate:

They use computational datasets, based on established models of beta cells acting in concert (electrically coupled) within an islet-like structure, to show that it is similarities in metabolic parameters rather than "structural" connections (ie proximity which subserves gap junction coupling) that drives functional network behaviour. Whilst the computational models are quite relevant, the fact that the parameters (eg connectivity coefficients) are quite different to what is measured experimentally, confirm the limitations of this model. Therefore it was important for the authors to back up this finding by performing both calcium and metabolic imaging of islet beta cells. These experimental data are reported to confirm that metabolic coupling was more strongly related to functional connectivity than gap junction coupling. However, a limitation here is that the metabolic imaging data confirmed a strong link between disconnected beta cells and low metabolic coupling but did not robustly show the opposite. Similarly, I was not convinced that the FRAP studies, which indirectly measured GJ ("structural") connections were powered well enough to be related to measures of beta cell connectivity.

The group goes on to provide further analytical and experimental data with a model of increasing loss of GJ connectivity (by calcium imaging islets from WT, heterozygous (50% GJ loss), and homozygous (100% loss). Given the former conclusion that it was metabolic not GJ connectivity that drives small world network behaviour, it was surprising to see such a great effect on the loss of hubs in the homs. That said, the analytical approaches in this model did help the authors confirm that the loss of gap junctions does not alter the preferential existence of beta cell connectivity and confirms the important contribution of metabolic "coupling". One perhaps can therefore conclude that there are two types of network behaviour in an islet (maybe more) and the field should move towards an understanding of overlapping network communities as has been done in brain networks.

Overall this is an extremely well-written paper which was a pleasure to read. This group has neatly and expertly provided both computational and experimental data to support the notion that it is metabolic but not "structural" ie GJ coupling that drives our observations of hubs and functional connectivity. However, there is still much work to do to understand whether this metabolic coupling is just a random epiphenomenon or somehow fated, the extent to which other elements of "structural" coupling - ie the presence of other endocrine cell types, the spatial distribution of paracrine hormone receptors, blood vessels and nerve terminals are also important.

We thank reviewer 3 for their positive comments, including the methodology, writing style, and the importance of this paper to the broader islet community. We thank the reviewer for their very in-depth and helpful comments. We have addressed each comment below and made significant changes to the manuscript according. We conducted more FRAP experiments and separated results into slow, fast, and mixed oscillations. We included analysis of an additional computational model that simulates slow calcium oscillations. Additionally, we substantially rewrote the paper to clarify that we are not referring to metabolic coupling and speak on the broader implications of network theory and our findings.

Reviewer #4 (Public Review):

This manuscript describes a complex, highly ambitious set of modeling and experimental studies that appear designed to compare the structural and functional properties of beta cell subpopulations within the islet network in terms of their influence on network synchronization. The authors conclude that the most functionally coupled cell subpopulations in the islet network are not those that are most structurally coupled via gap junctions but those that are most metabolically active.

Strengths of the paper include (1) its use of an interdisciplinary collection of methods including computer simulations, FRAP to monitor functional coupling by gap junctions, the monitoring of Ca2+ oscillations in single beta cells embedded in the network, and the use of sophisticated approaches from probability theory. Most of these methods have been used and validated previously. Unfortunately, however, it was not clear what the underlying premise of the paper actually is, despite many stated intentions, nor what about it is new compared to previous studies, an additional weakness.

Although the authors state that they are trying to answer 3 critical questions, it was not clear how important these questions are in terms of significance for the field. For example, they state that a major controversy in the field is whether network structure or network function mediates functional synchronization of beta cells within the islet. However, this question is not much debated. As an example, while it is known that there can be long-range functional coupling in islets, no workers in the field believe there is a physical structure within islets that mediates this, unlike the case for CNS neurons that are known to have long projections onto other neurons. Beta cells within the islets are locally coupled via gap junctions, as stated repeatedly by the authors but these mediate short-range coupling. Thus, there are clearly functional correlations over long ranges but no structures, only correlated activity. This weakness raises questions about the overall significance of the work, especially as it seems to reiterate ideas presented previously.

We thank reviewer 4 for their positive comments, including our multidisciplinary use of mathematical models and experimental imaging techniques. We have now included an additional model of slow oscillations (the Integrated Oscillator Model) to improve our conclusions. We also thank reviewer 4 for the insightful comments. We have carefully reviewed each comment and made significant changes to the manuscript accordingly. In particular, we have significantly rewritten the introduction and discussion attempting to clarify what is new in our manuscript and what is previously shown. Additionally, we agree with the reviewers’ sentiment that there is little debate over whether, for example, there are physical structures within the islet that mediate long-range functional connections. However, there is current debate over whether functional beta-cell subpopulations can dictate islet dynamics (see [11]–[13]). This debate can be framed by observing whether these functional subpopulations emerge from the islet due to physical connections (structural network) or something more nuisance (such as intrinsic dynamics). We have reframed the introduction and discussion to clarify this debate as well as more clearly state the premise of the paper.

Specific Comments

1). The authors state it is well accepted that the disruption of gap junctional coupling is a pathophysiological characteristic of diabetes, but this is not an opinion widely accepted by the field, although it has been proposed. The authors should scale back on such generalizations, or provide more compelling evidence to support such a claim.

Thank you for pointing this out, we have provided more specific citations and changes the wording from “well accepted” to “has been documented”. See Discussion page 13 lines 415-416.

2) The paper relies heavily on simulations performed using a version of the model of Cha et al (2011). While this is a reasonable model of fast bursting (e.g. oscillations having periods <1 min.), the Ca2+ oscillations that were recorded by the authors and shown in Fig. 2b of the manuscript are slow oscillations with periods of 5 min and not <1 min, which is a weakness of the model in the current context. Furthermore, the model outputs that are shown lack the well-known characteristics seen in real islets, such as fast-spiking occurring on prolonged plateaus, again as can be seen by comparing the simulated oscillations shown in Fig. 1d with those in Fig. 2b. It is recommended that the simulations be repeated using a more appropriate model of slow oscillations or at least using the model of Cha et al but employed to simulate in slower bursting.

The reviewer raises an important point and caveat associated with our simulated model and experimental data. This point was also made by other reviewers, and a similar response to this comment can be found elsewhere in response to reviewer 2 point 6. To address this comment, we have performed several additional experiments and analyses:

1) We collected additional Ca2+ (to identify the functional network and hubs) and FRAP data (to assess gap junction permeability) in islets which show either pure slow, pure fast, or mixed oscillations. We generated networks based on each time scale to compare with FRAP gap junction permeability data. We found that the conclusions of our first draft to be consistent across all oscillation types. There was no relationship between gap junction conductance, as approximated using FRAP, and normalized degree for slow (Figure 3j), fast (Figure 3 Supp 1d,e), or mixed (Figure 3 Supp 1g,h) oscillations. We also include discussion of these conclusions - See Results page 7 lines 184-186 and lines 188-191, Discussion page 12 lines 357-360.

2) We also performed additional simulations with a coupled ‘Integrated Oscillator Model’ which shows slow oscillations because of metabolic oscillations (Figure 2). We compared connectivity with gap junction coupling and underlying cell parameters. In this case, there is an association between functional and structural networks, with highly-connected hub cells showing higher gap junction conductance (Figure 2f) but also low KATP channel conductance (gKATP) (Figure 2e). However, there are some caveats to these findings – given the nature of the IOM model, we were limited to simulating smaller islets (260 cells) and less heterogeneity in the calcium traces was observed. Additional analysis suggests the greater association between functional and structural networks in this model was a result of the smaller islets, and the association was also dependent on threshold (unlike in the Cha-Noma fast oscillator model) robust. These limitations and results are discussed further (Discussion page 11 lines 344-354).

Additionally, in the IOM, the underlying cell dynamics of highly-connected hub cells are differentiated by KATP channel conductance (gKATP), which is different than in the fast oscillator model (differentiated by metabolism, kglyc). However this difference between models can be linked to differences in the way duty cycle is influenced by gKATP and kglyc (Figure 1h, Figure 2g). In each model there was a similar association between duty cycle and highly-connected hub cells. We also discuss these findings (Discussion page 11 lines 334-343).

Overall these results and discussion with respect to the coupled IOM oscillator model can be found in Figure 2, Results page 6 lines 128-156 and Discussion page 11 lines 332-354.

3) Much of the data analyzed whether obtained via simulation or through experiment seems to produce very small differences in the actual numbers obtained, as can be seen in the bar graphs shown in Figs. 1e,g for example (obtained from simulations), or Fig. 2j (obtained from experimental measurements). The authors should comment as to why such small differences are often seen as a result of their analyses throughout the manuscript and why also in many cases the observed variance is high. Related to the data shown, very few dots are shown in Figs. 1eg or Fig 4e and 4h even though these points were derived from simulations where 100s of runs could be carried out and many more points obtained for plotting. These are weaknesses unless specific and convincing explanations are provided.

We thank the reviewer for these comments, which are similar to those of reviewer 2 (point 4) and reviewer 3 (point 6). Indeed there is some variability between cells in both simulations and experiments related to the metabolic activity in hubs and non-hubs. The variability points to potentially other factors being involved in determining hubs beyond simply kglyc, including a minor role for gap junction coupling structural network and potentially cell position and other intrinsic factors. We now discuss this point – see Discussion page 12 lines 364-266.

The differences between hubs and nonhubs appear small because the value of kglyc is very small. For figure 1e, the average kglyc for nonhubs was 1.26x10-4 s-1 (which is the average of the distribution because most cells are non hubs) while the average kglyc for hubs was 1.4x10-4 s-1 which is about half of a standard deviation higher. The paired t-test controls for the small value of average kglyc.

For simulation data each of the 5 dots corresponds to a simulated islet averaged over 1000 cells (or 260 cells for coupled IOM). The computational resources are high to generate such data so it is not feasible to conduct 100s of runs. Again, we note the comparisons between hubs and non-hubs are paired, and we find statistically significant differences for kglyc in figure 1 using only 5 paired data points. That we find these differences indicates the substantial difference between hubs and non-hubs. This is further supported all effect sizes being much greater than 0.8 for all significantly different findings (Cha Noma - kglyc: 2.85, gcoup: 0.82) (IOM: gKATP: 1.27, gcoup: 2.94) – We have included these effect sizes in the captions see Figure 1 and 2 captions (pages 34, 36)

To consider all of the available data rather than the average across an entire islet, we created a kernel density estimate the kglyc for hubs and nonhubs created by concatenating every single cell in each of the five islets. A kstest results in a highly significant difference (P<0.0001) between these two distributions.

Author response image 1.

4) The data shown in Fig. 4i,j are intended to compare long-range synchronization at different distances along a string of coupled cells but the difference between the synchronized and unsynchronized cells for gcoup and Kglyc was subtle, very much so.

Thank you for pointing out these subtle differences. The y-axis scale for i and j is broad to allow us to represent all distances on a single plot. After correction for multiple comparison, the differences were still statistically significant. As the reviewer mentioned in point 3, each plot contains only five data points, each of which represent the average of a single simulated islet, therefore we are not concerned about statistical significance coming from too large of a sample size. We also checked the differences between synchronized and nonsynchronized cell pairs in figure 4 panels e and h (now figure 5 e, h). These are the same data as i and j but normalized such that all of the distances could be averaged together. We again found statistical significance between synchronized and non-synchronized cell pairs. As can be seen in Author response image 2 the difference between synchronized and non-synchronized cell pairs is greater than the variability between simulated islets. Thus, in this case the variability is not substantial.

Author response image 2.

5) The data shown in Fig. 5 for Cx36 knockout islets are used to assess the influence of gap junctional coupling, which is reasonable, but it would be reassuring to know that loss of this gene has no effects on the expression of other genes in the beta cell, especially genes involved with glucose metabolism.

This is an important point. Previous studies have assessed that no significant change in NAD(P)H is observed in Cx36 deficient islets – see Benninger et al J.Physiol 2011 [14]. Islet architecture is also retained. Further the insulin secretory response of dissociated Cx36 knockout beta cells is the same as that of dissociated wildtype beta cells, further indicating no significant defect in the intrinsic ability of the beta cell to release insulin – see Benninger et al J.Physiol 2011 [14]. We now Mention these findings in the discussion. See Discussion page 14 lines 459-464.

6) In many places throughout the paper, it is difficult to ascertain whether what is being shown is new vs. what has been shown previously in other studies. The paper would thus benefit strongly from added text highlighting the novelty here and not just restating what is known, for instance, that islets can exhibit small-world network properties. This detracts from the strengths of the paper and further makes it difficult to wade through. Even the finding here that metabolic characteristics of the beta cells can infer profound and influential functional coupling is not new, as the authors proposed as much many years ago. Again, this makes it difficult to distill what is new compared to what is mainly just being confirmed here, albeit using different methods.

Thank you for the suggestion, we have made significant modifications throughout the Introduction, Discussion and Results to be clearer about what is known from previous work and what is newly found in this manuscript.

Reviewer #5 (Public Review):

The authors use state-of-the-art computation, experiment, and current network analysis to try and disaggregate the impact of cellular metabolism driving cellular excitability and structural electrical connections through gap junctions on islet synchronization. They perform interesting simulations with a sophisticated mathematical model and compare them with closely associated experiments. This close association is impressive and is an excellent example of using mathematics to inform experiments and experimental results. The current conclusions, however, appear beyond the results presented. The use of functional connectivity is based on correlated calcium traces but is largely without an understood biophysical mechanism. This work aims to clarify such a mechanism between metabolism and structural connection and comes out on the side of metabolism driving the functional connectivity, but both are required and more nuanced conclusions should be drawn.

We thank reviewer 5 for their positive comments, including our multifaceted experimental and computational techniques. We also found the reviewers careful reading and thoughtful comments to be very helpful and we have worked to integrate each comment into our manuscript. It is evident from the reviewer comments that we did not clearly explain what was meant by our conclusions concerning the functional network reflecting metabolism rather than gap junctions. We have conducted significant rewriting to show that we are not concluding that communication (metabolic or electric) occurs due to conduits other than gap junctions. Rather, our data suggest that the functional network (which reflects calcium synchronization) reflects intrinsic dynamics of the cells, which include metabolic rates, more than individual gap junction connections.

References referred to in this response to reviewers document:

[1] A. Stožer et al., “Functional connectivity in islets of Langerhans from mouse pancreas tissue slices,” PLoS Comput Biol, vol. 9, no. 2, p. e1002923, 2013.

[2] N. L. Farnsworth, A. Hemmati, M. Pozzoli, and R. K. Benninger, “Fluorescence recovery after photobleaching reveals regulation and distribution of connexin36 gap junction coupling within mouse islets of Langerhans,” The Journal of physiology, vol. 592, no. 20, pp. 4431–4446, 2014.

[3] C.-L. Lei, J. A. Kellard, M. Hara, J. D. Johnson, B. Rodriguez, and L. J. Briant, “Beta-cell hubs maintain Ca2+ oscillations in human and mouse islet simulations,” Islets, vol. 10, no. 4, pp. 151–167, 2018.

[4] N. R. Johnston et al., “Beta cell hubs dictate pancreatic islet responses to glucose,” Cell metabolism, vol. 24, no. 3, pp. 389–401, 2016.

[5] V. Kravets et al., “Functional architecture of pancreatic islets identifies a population of first responder cells that drive the first-phase calcium response,” PLoS Biology, vol. 20, no. 9, p. e3001761, 2022.

[6] H. Ren et al., “Pancreatic α and β cells are globally phase-locked,” Nature Communications, vol. 13, no. 1, p. 3721, 2022.

[7] A. Stožer et al., “From Isles of Königsberg to Islets of Langerhans: Examining the function of the endocrine pancreas through network science,” Frontiers in Endocrinology, vol. 13, p. 922640, 2022.

[8] J. Zmazek et al., “Assessing different temporal scales of calcium dynamics in networks of beta cell populations,” Frontiers in physiology, vol. 12, p. 337, 2021.

[9] M. E. Corezola do Amaral et al., “Caloric restriction recovers impaired β-cell-β-cell gap junction coupling, calcium oscillation coordination, and insulin secretion in prediabetic mice,” American Journal of Physiology-Endocrinology and Metabolism, vol. 319, no. 4, pp. E709–E720, 2020.

[10] J. M. Dwulet, J. K. Briggs, and R. K. P. Benninger, “Small subpopulations of beta-cells do not drive islet oscillatory [Ca2+] dynamics via gap junction communication,” PLOS Computational Biology, vol. 17, no. 5, p. e1008948, May 2021, doi: 10.1371/journal.pcbi.1008948.

[11] B. E. Peercy and A. S. Sherman, “Do oscillations in pancreatic islets require pacemaker cells?,” Journal of Biosciences, vol. 47, no. 1, pp. 1–11, 2022.

[12] G. A. Rutter, N. Ninov, V. Salem, and D. J. Hodson, “Comment on Satin et al.‘Take me to your leader’: an electrophysiological appraisal of the role of hub cells in pancreatic islets. Diabetes 2020; 69: 830–836,” Diabetes, vol. 69, no. 9, pp. e10–e11, 2020.

[13] L. S. Satin and P. Rorsman, “Response to comment on satin et al.‘Take me to your leader’: An electrophysiological appraisal of the role of hub cells in pancreatic islets. Diabetes 2020; 69: 830–836,” Diabetes, vol. 69, no. 9, pp. e12–e13, 2020.

[14] R. K. Benninger, W. S. Head, M. Zhang, L. S. Satin, and D. W. Piston, “Gap junctions and other mechanisms of cell–cell communication regulate basal insulin secretion in the pancreatic islet,” The Journal of physiology, vol. 589, no. 22, pp. 5453–5466, 2011.

[15] R. Fried, Erectile dysfunction as a cardiovascular impairment. Academic Press, 2014. [16] T. Pipatpolkai, S. Usher, P. J. Stansfeld, and F. M. Ashcroft, “New insights into KATP channel gene mutations and neonatal diabetes mellitus,” Nature Reviews Endocrinology, vol. 16, no. 7, pp. 378–393, 2020.

[17] A. M. Notary, M. J. Westacott, T. H. Hraha, M. Pozzoli, and R. K. P. Benninger, “Decreases in Gap Junction Coupling Recovers Ca2+ and Insulin Secretion in Neonatal Diabetes Mellitus, Dependent on Beta Cell Heterogeneity and Noise,” PLOS Computational Biology, vol. 12, no. 9, p. e1005116, Sep. 2016, doi: 10.1371/journal.pcbi.1005116.

[18] J. V. Rocheleau, G. M. Walker, W. S. Head, O. P. McGuinness, and D. W. Piston, “Microfluidic glucose stimulation reveals limited coordination of intracellular Ca2+ activity oscillations in pancreatic islets,” Pro ceedings of the National Academy of Sciences, vol. 101, no. 35, pp. 12899–12903, 2004. [19] R. K. Benninger, M. Zhang, W. S. Head, L. S. Satin, and D. W. Piston, “Gap junction coupling and calcium waves in the pancreatic islet,” Biophysical journal, vol. 95, no. 11, pp. 5048–5061, 2008.

Author Response

Reviewer #1 (Public Review)

The documented findings may be explained by the artifact of task design and the way the signals were calculated: The vmPFC was the only ROI for which a positive correlation was found between BGA and mood rating and TML. Instead, most other regions showed negative correlation (inlc da-Insula, dorsolateral prefrontal cortex, the visual cortex, the motor cortex, the dorsomedial premotor cortex, the ventral somatosensory cortex, and the ventral inferior parietal lobule). This can be purely an artifact of task itself: In 25% of mood rating trials, subjects were presented with a question. They had to move the cursor from left (very bad) to the right (very good) along a continuous visual analog scale (100 steps) with left and right-hand response buttons. They even got a warning if they were slow. In 75% of trials, subjects saw none of this and the screen was just blank and the subjects rested.”

1) First of all, it is unclear if the 25% and 75% trials were mixed. I am assuming that they were not mixed as that could represent a fundamental mistake. The manuscript gives me the impression that this was not done (please clarify).

If by 25% and 75% trials the Reviewer means rating and no-rating trials then yes, they were intermixed (following on Vinckier et al. 2018). As explained in the initial manuscript, mood was rated every 3-7 trials (for a total of 25% of trials), and we used a computational model to interpolate mood (i.e., theoretical mood level) for the trials in between. This was implemented to avoid sampling mood systematically after every feedback and to test whether vmPFC and daIns represents mood continuously or just when it must be rated. We do not see how this could represent a fundamental mistake. Note that the associations between BGA and mood hold whether we use only rating trials, or only no-rating trials, or both types of trials.

To better explain how ratings and feedbacks were distributed across trials, we have added a supplementary figure that shows a representative example (Figure S1). This plot shows that ratings were collected independently of whether subjects were in high- or low-mood episodes. In other words, the alternance between rating and no-rating trials was orthogonal to the alternance between low- and high-mood episodes.

2) Assuming that they were not mixed and we are seeing the data from 75% of trials only. These trials would trigger increased BGA activity in the default mode areas such as the vmPFC, and opposite patterns in the salience, visual and motor areas. Hence the opposite correlations. The authors should just plot BGA activity across regions during rest trials and see if this was the case. That would provide a whole different interpretation.

Even if there were opposite correlations induced by the alternance between rating and no-rating trials, they would be orthogonal to mood fluctuations induced by positive and negative feedbacks. There is no way these putative opposite correlations could confound the correlation between BGA and mood, when restricted for instance to rating trials only. Anyway, what data show is not an opposite correlation between vmPFC and daIns (see figure R1 below) but that these two regions, when included as competing regressors in a same model, are both significant predictors of mood level. This could not be the case if vmPFC and daIns activities were just mirror reflections of a same factor (alternance of rating and no-rating trials).

We agree on the argument that performing a task may activate (increase BGA in) the daIns and deactivate (decrease BGA in) the vmPFC, but this average level of activity is not relevant for our study, which explores trial-to-trial fluctuations. It would only be problematic if the alternance between rating and no-rating trials was 1) correlated to mood levels and 2) inducing (anti)correlations between vmPFC and daIns BGA. The first assumption is false by construction of the design, as explained above, and the second assumption is empirically false, as shown below by the absence of correlation between daIns and vmPFC BGA. For each trial, we averaged BGA during the pre-stimulus time window (-4 to 0s) and tested the correlation between all possible pairs of vmPFC and daIns recording sites implanted in a same subject (n = 247 pairs of recording sites from 18 subjects). We observed no reliable correlation between the two brain regions, whether including only rest (no-rating) trials, only rating trials, or all trials together (see figure R1 below). On the contrary, the positive correlation between mood and vmPFC, as well as the negative correlation between mood and daIns, was observed in all cases (whether considering rest, rating, or all trials together).

Figure R1: Correlation between vmPFC and daIns activities. Bars show the correlation coefficients, averaged across pairs of recording sites, obtained when including all trials, only rest trials (no rating), or only mood-rating trials. The p-values were obtained using a two-sided, one-sample Student’s t-test on Fisher-transformed correlation coefficients. Note that performing the same analysis across subjects (instead of recording sites) yields the same result.

3) In addition, it is entirely unclear how the BGA in a given electrode was plotted. How is BGA normalized for each electrode? What is baseline here? Without understanding what baseline was used for this normalization, it is hard to follow the next section about the impact of the intracerebral activity on decision-making.

The normalization we used is neutral to the effect of interest. Details of BGA computation are given in the Methods section (lines 746-751):

“For each frequency band, this envelope signal (i.e., time varying amplitude) was divided by its mean across the entire recording session and multiplied by 100. This yields instantaneous envelope values expressed in percentage (%) of the mean. Finally, the envelope signals computed for each consecutive frequency band were averaged together to provide a single time series (the broadband gamma envelope) across the entire session. By construction, the mean value of that time series across the recording session is equal to 100.”

Then, BGA was simply z-scored over trials for every recording site. Thus, there was no baseline correction in the sense that there was no subtraction of pre-stimulus activity. We agree this would have been problematic, since we were precisely interested in the information carried by pre-stimulus activity. By z-scoring, we took as reference the mean activity over all trials.

We added the following sentence in the Methods section (lines 755-756):

“BGA was normalized for each recording site by z-scoring across trials.”

4) line 237: how was the correction for multiple comparisons done? Subject by subject, ROI by ROI, electrode by electrode? Please clarify.

The correction for multiple comparisons was done using a classic cluster-based permutation test (Maris & Ostenweld, 2007, J. Neurosci. Methods) performed at the level of ROI.

We have updated the section detailing this method in the manuscript (lines 807-818), as follows:

“For each ROI, a t-value was computed across all recording sites of the given ROI for each time point of the baseline window (-4 to 0 s before choice onset), independently of subject identity, using two-sided, one-sample, Student’s t-tests. For all GLMs, the statistical significance of each ROI was assessed through permutation tests. First, the pairing between responses and predictors across trials was shuffled randomly 300 times for each recording site. Second, we performed 60,000 random combinations of all contacts in a ROI, drawn from the 300 shuffles calculated previously for each site. The maximal cluster-level statistics (the maximal sum of t-values over contiguous time points exceeding a significance threshold of 0.05) were extracted for each combination to compute a “null” distribution of effect size across a time window from -4 to 0 s before choice onset (the baseline corresponding to the rest or mood assessment period). The p-value of each cluster in the original (non-shuffled) data was finally obtained by computing the proportion of clusters with higher statistics in the null distribution, and reported as the “cluster-level corrected” p-value (pcorr).”

Reviewer #2 (Public Review)

“This study used intracranial EEG to explore links between broad-band gamma oscillations and mood, and their impact on decisions. The topic is interesting and important. A major strength is the use of intracranial EEG (iEEG) techniques, which allowed the authors to obtain electrical signals directly from deep brain areas involved in decision making. With its precise temporal resolution, iEEG allowed the authors to study activity in specific frequency bands. While the results are potentially interesting, one major concern with the analysis procedure-specifically grouping of all data across all subjects and performing statistics across electrodes instead of across subjects-reduces enthusiasm for these findings. There is also a question about how mood impacts attentional state, which has already been shown to impact baseline (pre-stimulus) broad band gamma.”

Major comments

1)The number of subjects with contacts in vmPFC, daIns, and both vmPFC and daIns should be stated in the manuscript so the reader doesn't have to refer to the supplementary table to find this information.

These details have been added to the Results section (lines 236-242 and 258-262), as follows:

“The vmPFC (n = 91 sites from 20 subjects) was the only ROI for which we found a positive correlation (Figure 2b; Source data 1; Table S2) between BGA and both mood rating (best cluster: -1.37 to -1.04 s, sum(t(90)) = 122.3, pcorr = 0.010) and TML (best cluster: -0.57 to -0.13 s, sum(t(90)) = 132.4, pcorr = 8.10-3). Conversely, we found a negative correlation in a larger brain network encompassing the daIns (n = 86 sites from 28 subjects, Figure 2b; Source data 1; Table S2), in which BGA was negatively associated with both mood rating (best cluster: -3.36 to -2.51 s, sum(t(85)) = -325.8, pcorr < 1.7.10-5) and TML (best cluster: -3.13 to -2.72 s, sum(t(85)) = -136.4, pcorr = 9.10-3). (…) In order to obtain the time course of mood expression in the two ROIs (Figure 2c), we performed regressions between TML and BGA from all possible pairs of vmPFC and daIns recording sites recorded in a same subject (n = 247 pairs of recording sites from 18 subjects, see Methods) and tested the regression estimates across pairs within each ROI at each time point.”

2) Effects shown in figs 2 and 3 are combined across subjects. We don't know the effective sample size for the comparisons being made, and the effects shown could be driven by just a few subjects. If the authors compute trial-wise regressions between mood and BGA for each subject, and then perform the statistics across subjects instead of across electrodes, do these results still pan out?

Yes, we have redone the analyses at the group level to get statistics across subjects (see response to essential revisions). All main results remained significant or borderline. In these group-level random-effect analyses, data points are subject-wise BGA averaged across recording sites (within the temporal cluster identified with the fixed-effect approach). We have incorporated these analyses into the manuscript as a supplementary table (Table S4). However, these statistics across subjects are less standard in the field of electrophysiology, as they are both underpowered and unadjusted for sampling bias (because the same weight is given to subjects with 1 or 10 recording sites in the ROI), so we prefer to keep the usual statistics across recording sites in the main text.

These analyses have been incorporated into the Results section (lines 355-357), as follows:

“We also verified that the main findings of this study remained significant (or borderline) when using group-level random-effects analyses (Table S4, see methods), even if this approach is underpowered and unadjusted for sampling bias (some subjects having very few recording sites in the relevant ROI).”

The methods section has also been edited, as follows (lines 831-835):

“To test the association between BGA and mood, TML or choice at the group level (using random-effects analyses), we performed the same linear regression as described in the electrophysiological analyses section on BGA averaged over the best time cluster (identified by the fixed-effects approach) and across all recording sites of a given subjects located in the relevant ROI. We then conducted a two-sided, one-sample Student's t-test on the resulting regression estimates (Table S4).”

3) Furthermore, how many of the subjects show statistically significant regressions between BGA and mood at any electrode? For example, the error bars in fig 2b are across electrodes. How would this figure look if error bars indicated variance across subjects instead?

Depending on the metrics (mood rating or theoretical mood level), statistically significant regressions between BGA and mood was observed in 4 to 6 subjects for the vmPFC and 5 to 9 subjects in the daIns. We provide these numbers to satisfy the Reviewer’s request, but we do not see what statistical inference they could inform (inferences based on number of data points above and below significance threshold are clearly wrong). To satisfy the other request, we have reproduced below Fig. 2B with error bars indicating variance across subjects and not recording sites (Figure R2). Again, to make an inference about a neural representation at the population level, the relevant samples are recording sites, not subjects. All monkey electrophysiology studies base their inferences on the variance across neurons (typically coming from 2 or 3 monkeys pooled together).

Figure R2: Reproduction of Figure 2B with lower panels indicating mean and variance across subjects instead of recording sites (upper panels). Blue: vmPFC, red: daIns. Bold lines indicate significant clusters (p < 0.05).

4) In panel f, we can see that a large number of sites in both ROIs show correlations in the opposite direction to the reported effects. How can this be explained? How do these distributions of effects in electrodes correspond to distributions of effects in individual subjects?

In our experience, this kind of pattern is observed in any biological dataset, so we do not understand what the Reviewer wants us to explain. It is simply the case for any significant effect across samples, the distribution would include some samples with effects in the opposite direction. If there were no effects in the opposite direction, nobody would need statistics to know whether the observed distribution is different from the null distribution. In our case, the variability might have arisen from different sources of noise (in mood estimate, in BGA recording, in stochastic fluctuations of pre-stimulus activity, in the link between mood and BGA that may be depends on unknown factors, etc.) This variability has been typically masked because until recently, effects of interest were plotted as means with error bars. The variability is more apparent when plotting individual samples, as we did. It is visually amplified by the fact that outliers are as salient as data points close to the mean, which are way more numerous but superimposed. We have replotted below the panel f with data points being subjects instead of recording sites (Figure R3).

Figure R3: Reproduction of Figure 2F with lower panels showing the distribution, of regression estimates over subjects instead of recording sites (upper panels). Blue: vmPFC, red: daIns. Note that this is the only analysis which failed to reach significance using a group-level random-effect approach. This is not surprising as this approach is underpowered (perhaps in particular for this analysis over a [-4 to 0 s] pre-choice time window) and unadjusted for sampling bias (some subjects having very few recording sites in the relevant ROI).

5) Baseline (pre-stimulus) gamma amplitudes have been shown to be related to attentional states. Could these effects be driven by attention rather than mood? The relationship between mood and decisions may be more complex than the authors describe, and could impact other cognitive factors such as attention, which have already been shown to impact baseline broad-band gamma.

We agree with the Reviewer that the relationships between mood and decisions are certainly more complex in reality than in our model, which is obviously a simplification, as any model is. We also acknowledge that pre-stimulus gamma activity is modulated by fluctuations in attention. However, what was measured and related to BGA in our study is mood level, so it remains unclear what reason could support the claim that the effects may have been driven by attention. A global shift in attentional state (like being more vigilant when in a good or bad mood) would not explain the specific effects we observed (making more or less risky choices). If the Reviewer means that subjects might have paid more attention to gain prospects when in a good mood, and to loss prospects when in a bad mood, then we agree this is a possibility. Note however that the difference between this scenario and our description of the results (subjects put more weight on gain/loss prospect when in a good/bad mood) would be quite subtle. We have nevertheless incorporated this nuance in the discussion (lines 494-496):

“This result makes the link with the idea that we may see a glass half-full or half-empty when we are in a good or bad mood, possibly because we pay more attention to positive or negative aspects.”

6) The authors used a bipolar montage reference. Would it be possible that effects in low frequencies are dampened because of the bipolar reference instead of common average reference?

This is unlikely, because the use of a common average reference montage has been shown to significantly increase the number of channels exhibiting task-related high-frequency activity (BGA), but not the number of channels exhibiting task-related low-frequency activity (see Li et al., 2018, Figure 5A-B). In addition, using a monopolar configuration would also have the disadvantage of significantly increasing the correlations between channels (compared to a bipolar montage). This would have therefore artificially induced task-related effects in other channels due to volume conduction effects (Li et al., 2018; Mercier et al., 2017).

Reviewer #3 (Public Review):

In this interesting paper, Cecchi et al. collected intracerebral EEG data from patients performing decision-making tasks in order to study how patient's trial-by-trial mood fluctuations affect their neural computation underlying risky choices. They found that the broadband gamma activity in vmPFC and dorsal anterior Insula (daIns) are distinctively correlated with the patient's mood and their choice. I found the results very interesting. This study certainly will be an important contribution to cognitive and computational neuroscience, especially how the brain may encode mood and associate it to decisions.

Major comments

1) The authors showed that the mood is positively correlated in vmPFC on high mood trials alone and negatively correlated daIns in low mood trials alone. This is interesting. But those are the trials in which these regions' activity predict choice (using the residual of choice model fit)?

This is an excellent point. The intuition of Reviewer 3 was correct. To test it, we performed a complementary analysis in which we regressed choice (model fit residuals) against BGA, separately for low vs. high mood trials (median-split). This analysis revealed that in the vmPFC, BGA during high mood trials positively predicted choices whereas in the daIns, BGA during low mood trials negatively predicted choices.

We have added the following paragraph in the Results section (lines 328-337):

“Taken together, these results mean that vmPFC and daIns baseline BGA not only express mood in opposite fashion, but also had opposite influence on upcoming choice. To clarify which trials contributed to the significant association between choice and BGA, we separately regressed the residuals of choice model fit against BGA across either high- or low-mood trials (median split on TML; Figure 3b). In the vmPFC, regression estimates were significantly positive for high-mood trials only (high TML = 0.06 ± 0.01, t(90) = 5.64, p = 2.10-7; two-sided, one-sample, Student’s t-test), not for low-mood trials. Conversely, in the daIns, regression estimates only reached significance for low-mood trials (low TML = -0.05 ± 0.01, t(85) = -4.63, p = 1.10-5), not for high-mood trials. This double dissociation suggests that the vmPFC positively predicts choice when mood gets better than average, and the daIns negatively predicts choice when mood gets worse than average.”

Also, Figure 3 has been modified accordingly.

2) It would be helpful to see how high-mood trials and low-mood trials are distributed. Are they clustered or more intermixed?

We thank the Reviewer for the suggestion. To provide a more detailed view on how feedback history shaped mood ratings and TML, we added a supplementary figure that shows a representative example (Figure S1).

3) I am not sure how I should reconcile the above finding of the correlation between mood and BGA on high-mood vs. low-mood trials, and the results about how high vs. low baseline BGA predict choice. I may have missed something related to this in the discussion section, but could you clarify?

Following the Reviewer’s suggestion, we now demonstrate that the vmPFC positively predicts choice when mood gets better than average, and the daIns negatively predicts choice when mood gets worse than average (see response to first point).

To clarify this, we have added the following paragraph in the discussion (lines 461-469), and a schematic figure summarizing the main findings (Figure 4).

“Choice to accept or reject the challenge in our task was significantly modulated by the three attributes displayed on screen: gain prospect (in case of success), loss prospect (in case of failure) and difficulty of the challenge. We combined the three attributes using a standard expected utility model and examined the residuals after removing the variance explained by the model. Those residuals were significantly impacted by mood level, meaning that on top of the other factors, good / bad mood inclined subjects to accept / reject the challenge. The same was true for neural correlates of mood: higher baseline BGA in the vmPFC / daIns was both predicted by good / bad mood and associated to higher accept / reject rates, relative to predictions of the choice model. Thus, different mood levels might translate into different brain states that predispose subjects to make risky or safe decisions (Figure 4).”

Author Response

Reviewer #1 (Public Review):

This paper presents an interesting data set from historic Western Eurasia and North Africa. Overall, I commend the authors for presenting a comprehensive paper that focuses the data analysis of a large project on the major points, and that is easy to follow and well-written. Thus, I have no major comments on how the data was generated, or is presented. Paradoxically, historical periods are undersampled for ancient DNA, and so I think this data will be useful. The presentation is clever in that it focuses on a few interesting cases that highlight the breadth of the data.

The analysis is likewise innovative, with a focus on detecting "outliers" that are atypical for the genetic context where they were found. This is mainly achieved by using PCA and qpAdm, established tools, in a novel way. Here I do have some concerns about technical aspects, where I think some additional work could greatly strengthen the major claims made, and lay out if and how the analysis framework presented here could be applied in other work.

clustering analysis

I have trouble following what exactly is going on here (particularly since the cited Fernandes et al. paper is also very ambiguous about what exactly is done, and doesn't provide a validation of this method). My understanding is the following: the goal is to test whether a pair of individuals (lets call them I1 and I2) are indistinguishable from each other, when we compare them to a set of reference populations. Formally, this is done by testing whether all statistics of the form F4(Ref_i, Ref_j; I1, I2) = 0, i.e. the difference between I1 and I2 is orthogonal to the space of reference populations, or that you test whether I1 and I2 project to the same point in the space of reference populations (which should be a subset of the PCA-space). Is this true? If so, I think it could be very helpful if you added a technical description of what precisely is done, and some validation on how well this framework works.

We agree that the previous description of our workflow was lacking, and have substantially improved the description of the entire pipeline (Methods, section “Modeling ancestry and identifying outliers using qpAdm”), making it clearer and more descriptive. To further improve clarity, we have also unified our use of methodology and replaced all mentions of “qpWave” with “qpAdm”. In the reworked Methods section mentioned above, we added a discussion on how these tests are equivalent in certain settings, and describe which test we are exactly doing for our pairwise individual comparisons, as well as for all other qpAdm tests downstream of cluster discovery. In addition, we now include an additional appendix document (Appendix 4) which, for each region, shows the results from our individual-based qpAdm analysis and clustering in the form of heatmaps, in addition to showing the clusters projected into PC space.

An independent concern is the transformation from p-values to distances. I am in particular worried about i) biases due to potentially different numbers of SNPs in different samples and ii) whether the resulting matrix is actually a sensible distance matrix (e.g. additive and satisfies the triangle inequality). To me, a summary that doesn't depend on data quality, like the F2-distance in the reference space (i.e. the sum of all F4-statistics, or an orthogonalized version thereof) would be easier to interpret. At the very least, it would be nice to show some intermediate results of this clustering step on at least a subset of the data, so that the reader can verify that the qpWave-statistics and their resulting p-values make sense.

We agree that calling the matrix generated from p-values a “distance matrix” is a misnomer, as it does not satisfy the triangle inequality, for example. We still believe that our clustering generates sensible results, as UPGMA simply allows us to project a positive, symmetric matrix to a tree, which we can then use, given some cut-off, to define clusters. To make this distinction clear, we now refer to the resulting matrix as a “dissimilarity matrix” instead. As mentioned above, we now also include a supplementary figure for each region visualizing the clustering results.

Regarding the concerns about p-values conflating both signal and power, we employ a stringent minimum SNP coverage filter for these analyses to avoid extremely-low coverage samples being separated out (min. SNPs covered: 100,000). In addition, we now show that cluster size and downstream outlier status do not depend on SNP coverage (Figure 2 - Suppl. 3).

The methodological concerns lead me to some questions about the data analysis. For example, in Fig2, Supp 2, very commonly outliers lie right on top of a projected cluster. To my understanding, apart from using a different reference set, the approach using qpWave is equivalent to using a PCA-based clustering and so I would expect very high concordance between the approaches. One possibility could be that the differences are only visible on higher PCs, but since that data is not displayed, the reader is left wondering. I think it would be very helpful to present a more detailed analysis for some of these "surprising" clustering where the PCA disagrees with the clustering so that suspicions that e.g. low-coverage samples might be separated out more often could be laid to rest.

To reduce the risk of artifactual clusters resulting from our pipeline, we devised a set of QC metrics (described in detail below) on the individuals and clusters we identified as outliers. Driven by these metrics, we implemented some changes to our outlier detection pipeline that we now describe in substantially more detail in the Methods (see comment above). Since the pipeline involves running many thousands of qpAdm analyses, it is difficult to manually check every step for all samples – instead, we focused our QC efforts on the outliers identified at the end of the pipeline. To assess outlier quality we used the following metrics, in addition to manual inspection:

First, for an individual identified as an outlier at the end of the pipeline, we check its fraction of non-rejected hypotheses across all comparisons within a region. The rationale here is that by definition, an outlier shouldn’t cluster with many other samples within its region, so a majority of hypotheses should be rejected (corresponding to gray and yellow regions in the heatmaps, Appendix 4). Through our improvements to the pipeline, the fraction of non-rejected hypotheses was reduced from an average of 5.3% (median 1.1%) to an average of 3.8% (median 0.6%), while going from 107 to 111 outliers across all regions.

Second, we wanted to make sure that outlier status was not affected by the inclusion of pre-historic individuals in our clustering step within regions. To represent majority ancestries that might have been present in a region in the past, we included Bronze and Copper Age individuals in the clustering analysis. We found that including these individuals in the pairwise analysis and clustering improved the clusters overall. However, to ensure that their inclusion did not bias the downstream identification of outliers, we also recalculated the clustering without these individuals. We inspected whether an individual identified as an outlier would be part of a majority cluster in the absence of Bronze and Copper Age individuals, which was not the case (see also the updated Methods section for more details on how we handle time periods within regions).

In response to the “surprising” outliers based on the PCA visualizations in Figure 2, Supplement 2: with our updated outlier pipeline, some of these have disappeared, for example in Western and Northern Europe. However, in some regions the phenomenon remains. We are confident this isn’t a coverage effect, as we’ve compared the coverage between outliers and non-outliers across all clusters (see previous comment, Figure 2 - Suppl. 3), as well as specifically for “surprising” outliers compared to contemporary non-outliers – none of which showed any differences in the coverage distributions of “surprising” outliers (Author response images 1 and 2). In addition, we believe that the quality metrics we outline above were helpful in minimizing artifactual associations of samples with clusters, which could influence their downstream outlier status. As such, we think it is likely that the qpAdm analysis does detect a real difference between these sets of samples, even though they project close to each other in PCA space. This could be the result of an actual biological difference hidden from PCA by the differences in reference space (see also the reply to the following comment). Still, we cannot fully rule out the possibility of latent technical biases that we were not able to account for, so we do not claim the outlier pipeline is fully devoid of false positives. Nevertheless, we believe our pipeline is helpful in uncovering true, recent, long-range dispersers in a high-throughput and automated manner, which is necessary to glean this type of insight from hundreds of samples across a dozen different regions.

Author response image 1.

SNP coverage comparison between outliers and non-outliers in region-period pairings with “surprising” outliers (t-test p-value: 0.242).

Author response image 2.

PCA projection (left) and SNP coverage comparison (right) for “surprising” outliers and surrounding non-outliers in Italy_IRLA.

One way the presentation could be improved would be to be more consistent in what a suitable reference data set is. The PCAs (Fig2, S1 and S2, and Fig6) argue that it makes most sense to present ancient data relative to present-day genetic variation, but the qpWave and qpAdm analysis compare the historic data to that of older populations. Granted, this is a common issue with ancient DNA papers, but the advantage of using a consistent reference data set is that the analyses become directly comparable, and the reader wouldn't have to wonder whether any discrepancies in the two ways of presenting the data are just due to the reference set.

While it is true that some of the discrepancies are difficult to interpret, we believe that both views of the data are valuable and provide complementary insights. We considered three aspects in our decision to use both reference spaces: (1) conventions in the field (including making the results accessible to others), (2) interpretability, and (3) technical rigor.

Projecting historical genomes into the present-day PCA space allows for a convenient visualization that is common in the field of ancient DNA and exhibits an established connection to geographic space that is easy to interpret. This is true especially for more recent ancient and historical genomes, as spatial population structure approaches that of present day. However, there are two challenges: (1) a two-dimensional representation of a fairly high-dimensional ancestry space necessarily incurs some amount of information loss and (2) we know that some axes of genetic variation are not well-represented by the present-day PCA space. This is evident, for example, by projecting our qpAdm reference populations into the present-day PCA, where some ancestries which we know to be quite differentiated project closely together (Author response image 3). Despite this limitation, we continue to use the PCA representation as it is well resolved for visualization and maximizes geographical correspondence across Eurasia.

On the other hand, the qpAdm reference space (used in clustering and outlier detection) has higher resolution to distinguish ancestries by more comprehensively capturing the fairly high-dimensional space of different ancestries. This includes many ancestries that are not well resolved in the present-day PCA space, yet are relevant to our sample set, for example distinguishing Iranian Neolithic ancestry against ancestries from further into central and east Asia, as well as distinguishing between North African and Middle Eastern ancestries (Author response image 3).

To investigate the differences between these two reference spaces, we chose pairwise outgroup-f3 statistics (to Mbuti) as a pairwise similarity metric representing the reference space of f-statistics and qpAdm in a way that’s minimally affected by population-specific drift. We related this similarity measure to the euclidean distance on the first two PCs between the same set of populations (Author response image 4). This analysis shows that while there is almost a linear correspondence between these pairwise measures for some populations, others comparisons fall off the diagonal in a manner consistent with PCA projection (Author response image 3), where samples are close together in PCA but not very similar according to outgroup-f3. Taken together, these analyses highlight the non-equivalence of the two reference spaces.

In addition, we chose to base our analysis pipeline on the f-statistics framework to (1) afford us a more principled framework to disentangle ancestries among samples and clusters within and across regions (using 1-component vs. 2-component models of admixture), while (2) keeping a consistent, representative reference set for all analyses that were part of the primary pipeline. Meanwhile, we still use the present-day PCA space for interpretable visualization.

Author response image 3.

Projection of qpAdm reference population individuals into present-day PCA.

Author response image 4.

Comparison of pairwise PCA projection distance to outgroup-f3 similarity across all qpAdm reference population individuals. PCA projection distance was calculated as the euclidean distance on the first two principal components. Outgroup-f3 statistics were calculated relative to Mbuti, which is itself also a qpAdm reference population. Both panels show the same data, but each point is colored by either of the two reference populations involved in the pairwise comparison.

PCA over time

It is a very interesting observation that the Fst-vs distance curve does not appear to change after the bronze age. However, I wonder if the comparison of the PCA to the projection could be solidified. In particular, it is not obvious to me how to compare Fig 6 B and C, since the data in C is projected onto that in Fig B, and so we are viewing the historic samples in the context of the present-day ones. Thus, to me, this suggests that ancient samples are most closely related to the folks that contribute to present-day people that roughly live in the same geographic location, at least for the middle east, north Africa and the Baltics, the three regions where the projections are well resolved. Ideally, it would be nice to have independent PCAs (something F-stats based, or using probabilistic PCA or some other framework that allows for missingness). Alternatively, it could be helpful to quantify the similarity and projection error.

The fact that historical period individuals are “most closely related to the folks that contribute to present-day people that roughly live in the same geographic location” is exactly the point we were hoping to make with Figures 6 B and C. We do realize, however, that the fact that one set of samples is projected into the PC space established by the other may suggest that this is an obvious result. To make it more clear that it is not, we added an additional panel to Figure 6, which shows pre-historical samples projected into the present-day PC space. This figure shows that pre-historical individuals project all across the PCA space and often outside of present-day diversity, with degraded correlation of geographic location and projection location (see also Author response image 5). This illustrates the contrast we were hoping to communicate, where projection locations of historical individuals start to “settle” close to present-day individuals from similar geographic locations, especially in contrast with pre-historic individuals.

Author response image 5.

Comparing geographic distance to PCA distance between pairs of historical and pre-historical individuals matched by geographic space. For each historical period individual we selected the closest pre-historical individual by geographic distance in an effort to match the distributions of pairwise geographic distance across the two time periods (left). For these distributions of individuals matched by geographic distance, we then queried the euclidean distance between their projection locations in the first two principal components (right).

Author Response

Reviewer #3 (Public Review):

The authors explore the use of SRT as a host-directed therapy for use in combination with other first-line TB antibiotics. This manuscript is of substantial importance since TB is a major world health concern, and there is growing interest in the development of host-directed therapies to augment existing therapies for TB. Demonstrating the effectiveness of adding an FDA-approved drug to existing cocktails of anti-TB drugs has potentially exciting implications.

The manuscript is bolstered by their use of multiple in vitro and in vivo models of infection, as well as a clinically relevant strain of TB. While their findings generally support the use of SRT as an effective HDT/treatment, the mechanistic details underlying the effectiveness of SRT remain somewhat obscure, and as presented, the in vitro experiments support more limited conclusions.

Major concerns:

In vitro studies (i.e. bacterial culture) were only performed with SRT up to 6 uM while the cultured cell experiments used a range up to 20 uM. 5 uM had almost no effect on the viability/growth of Mtb in macrophages. The authors should use the same concentrations in vitro as their macrophage studies to test whether SRT directly impacts Mtb viability to be able to rule in/out that SRT does not impact Mtb viability when cultured.

We haven’t seen any appreciable decrease in the growth of Mtb at upto 20M in in vitro experiments, nearly 30-40% restriction after 8 days of culture. We used in combination of HR a lower dose of 6mM in combination with HR to offset the effect of minimal SRT inhibitory effects so that only the effect of SRT is understood.

The mechanism of action of SRT during TB infection and the conclusions drawn by the authors are not supported by the limited experimentation. SRT is presented as an antagonist of polyI:C-induced type I IFNs, but during TB infection, cytosolic DNA sensing via the cGAS/STING axis constitutes the major pathway through which type I IFNs are induced in macrophages.

To offer more support that SRT inhibits type I IFN, the authors should consider measuring the the actual amount of type I IFN using an IFNb ELISA. Additionally, the authors should use human/mouse primary macrophages (not just THP1 reporter cells) and measure transcript levels (at key time points post infection) and protein levels of type I IFN and other proinflammatory mediators (e.g. TNFa, IL-1, IL-6) +/- SRT to determine if SRT is specific to the type I IFN response. If this is indeed the case, other NFkB genes/cytokines should not be impacted.

Moreover, to draw the conclusion that "augmentation property of SRT is due to its ability to inhibit IFN signalling" a set of experiments using an IFN blocking antibody would enhance Figure 2, as both cGAS and STING KO macs have significant differences in basal gene expression and their ability to respond to innate immune stimuli.

Because the first half of the paper focuses on type I IFNs during macrophage infection to explain the mechanism of action for SRT, additional analysis of the mouse infections to examine levels of type I IFNs, as well as IL-1B and IFN-g (in serum/tissues?), is important for connecting the two halves of the manuscript. The in vivo data would also be strengthened by quantitative analysis of histological changes by, for example, blinded pathology scoring. This type of quantitation would also permit statistical analyses of this important pathology readout.

We have performed analyse of tissue cytokine levels and did not see stark differences in the levels between HRZE and HRZES at two time points of 4 and 8weeks post treatment (Figure below). We feel that such studies would need a more comprehensive analyses of the immunological response induced in the host by the treatment at multiple time points. Such studies would be part of a more focussed plan in the future proposals and manuscripts. We have also conducted a manual scoring of the lesions between the groups and have recorded this data in the manuscript (Fig.4-figure supplement 1)

The authors conclude that SRT functions through an inflammasome-related function, but this conclusion requires further support of actual inflammasome activation, such as IL-1B secretion by ELISA or IL-1B processing by western blot analysis, rather than Il1b gene expression alone. Additional functional readouts of inflammasome activation like cell death assays would also strengthen this conclusion.

We thank the reviewer for these suggestions. These studies are currently underway and will be part of a future manuscript detailing the mechanistics of SRT mediated increase in antibiotic efficacy.

What strain of TB was used in these studies? The results and methods do not indicate the strain used, which is critical to know since different strains have varying pathogenesis phenotypes.

We have used Mtb Erdman for routine drug sensitive and N73 for the drug tolerant studies. This has been added in the text.

Minor concerns:

It might be worth consistently using the more common INH and RIF abbreviations to increase the clarity/readability of the MS and figures.

We have used the conventional clinical abbreviations used for INH and Rifampicin What is the physiological concentration of SRT when taken for depression and how does that compare to the concentrations used in vitro? Are the in vitro concentrations feasible to achieve in patients?

In Figure 3B, why is there a spike in TNF-a in the HRS treated cells only at 42h?

The authors wish to thank the reviewer for this query. We have reanalysed the data and have depicted the modified figures in the current text version. The spike at 42H for TNF was an oversight and due to an erroneous representation of the values in the figure.

Was statistical analysis performed on the data in Figure 3B and D?

Yes, we have incorporated this information in the modified figure.

A description/discussion of the different mouse strains use in infection - what benefits each has as a model and why several were used - would help convey the impact of the in vivo studies.

These have been incorporated in the text. A discussion of the mouse strains and their immunopathology in infection has been included in the text.

Since antibiotics and SRT were administered ad libitum, how did the authors ensure that mice took enough of the antibiotics and especially SRT? Is it known whether these drugs affect the water taste enough to affect a mouse's willingness to drink them?

We preferred the use of ad libitum delivery of TB drugs in drinking water as used in the previous studies by Vilchèze et .al, 2018 Antimicrob Agents Chemother 23;62(3):e02165-17. To avoid non drinking, we used 5% glucose in the water of all animals including the non-antibiotic treated groups. We also followed the uptake of water during the treatment and found comparable levels of usage between the groups.

Was statistical analysis performed on time-to-death experiments?

Because of the inherent differences in the susceptibility and response between males and females C3HEBFEJ mice, we did not perform statistical analyses between the groups.

Were CFUs measured in mice from Figure 4 to determine empirically how effective the antibiotic treatments were? And if SRT impacted their effectiveness?

We have not tested the effect of SRT on bacterial burdens on bacteria treated with HR alone as these studies were aimed at deciphering chronic pathology. We have tested the effect on bacterial loads in the C3HEBFEJ model with the four-drug therapy and the C57BL6 and Balbc models of infection.

The H&E images could use some additional labels to more easily discern what groups they belong to.

These have been incorporated in the figure.

Author Response

Reviewer #1 (Public Review):

This is a carefully-conducted fMRI study looking at how neural representations in the hippocampus, entorhinal cortex, and ventromedial prefrontal cortex change as a function of local and global spatial learning. Collectively, the results from the study provide valuable additional constraints on our understanding of representational change in the medial temporal lobes and spatial learning. The most notable finding is that representational similarity in the hippocampus post-local-learning (but prior to any global navigation trials) predicts the efficiency of subsequent global navigation.

Strengths:

The paper has several strengths. It uses a clever two-phase paradigm that makes it possible to track how participants learn local structure as well as how they piece together global structure based on exposure to local environments. Using this paradigm, the authors show that - after local learning - hippocampal representations of landmarks that appeared within the same local environment show differentiation (i.e., neural similarity is higher for more distant landmarks) but landmarks that appeared in different local environments show the opposite pattern of results (i.e., neural similarity is lower for more distant landmarks); after participants have the opportunity to navigate globally, the latter finding goes away (i.e., neural similarity for landmarks that occurred in different local environments is no longer influenced by the distance between landmarks). Lastly, the authors show that the degree of hippocampal sensitivity to global distance after local-only learning (but before participants have the opportunity to navigate globally) negatively predicts subsequent global navigation efficiency. Taken together, these results meaningfully extend the space of data that can be used to constrain theories of MTL contributions to spatial learning.

We appreciate Dr. Norman’s generous feedback here along with his other insightful comments. Please see below for a point-by-point response. We note that responses to a number of Dr. Norman’s points were surfaced by the Editor as Essential revisions; as such, in a number of instances in the point-by-point below we direct Dr. Norman to our responses above under the Essential revisions section.

Weaknesses:

General comment 1: The study has an exploratory feel, in the sense that - for the most part - the authors do not set forth specific predictions or hypotheses regarding the results they expected to obtain. When hypotheses are listed, they are phrased in a general way (e.g., "We hypothesized that we would find evidence for both integration and differentiation emerging at the same time points across learning, as participants build local and global representations of the virtual environment", and "We hypothesized that there would be a change in EC and hippocampal pattern similarity for items located on the same track vs. items located on different tracks" - this does not specify what the change will be and whether the change is expected to be different for EC vs. hippocampus). I should emphasize that this is not, unto itself, a weakness of the study, and it appears that the authors have corrected for multiple comparisons (encompassing the range of outcomes explored) throughout the paper. However, at times it was unclear what "denominator" was being used for the multiple comparisons corrections (i.e., what was the full space of analysis options that was being corrected for) - it would be helpful if the authors could specify this more concretely, throughout the paper.

We appreciate this guidance and the importance of these points. We have taken a number of steps to clarify our hypotheses, we now distinguish a priori predictions from exploratory analyses, and we now explicitly indicate throughout the manuscript how we corrected for multiple comparisons. For full details, please see above for our response to Essential Revisions General comment #1.

General comment 2: Some of the analyses featured prominently in the paper (e.g., interactions between context and scan in EC) did not pass multiple comparisons correction. I think it's fine to include these results in the paper, but it should be made clear whenever they are mentioned that the results were not significant after multiple comparisons correction (e.g., in the discussion, the authors say "learning restructures representations in the hippocampus and in the EC", but in that sentence, they don't mention that the EC results fail to pass multiple comparisons correction).

Thank you for encouraging greater clarity here. As noted directly above, we now explicitly indicate our a priori predictions, we state explicitly which results survive multiple comparisons correction, and we added necessary caveats for effects that should be interpreted with caution.

General comment 3: The authors describe the "flat" pattern across the distance 2, 3, and 4 conditions in Figure 4c (post-global navigation) and in Figure 5b (in the "more efficient" group) as indicating integration. However, this flat pattern across 2, 3, and 4 (unto itself) could simply indicate that the region is insensitive to location - is there some other evidence that the authors could bring to bear on the claim that this truly reflects integration? Relatedly, in the discussion, the authors say "the data suggest that, prior to Global Navigation, LEs had integrated only the nearest landmarks located on different tracks (link distance 2)" - what is the basis for this claim? Considered on its own, the fact that similarity was high for link distance 2 does not indicate that integration took place. If the authors cannot get more direct evidence for integration, it might be useful for them to hedge a bit more in how they interpret the results (the finding is still very interesting, regardless of its cause).

Based on the outcomes of additional behavioral and neural analyses that were helpfully suggested by reviewers, we revised discussion of this aspect of the data. Please see our response above under Essential Revisions General comment #4 for full details of the changes made to the manuscript.

Reviewer #2 (Public Review):

This paper presents evidence of neural pattern differentiation (using representational similarity analysis) following extensive experience navigating in virtual reality, building up from individual tracks to an overall environment. The question of how neural patterns are reorganized following novel experiences and learning to integrate across them is a timely and interesting one. The task is carefully designed and the analytic setup is well-motivated. The experimental approach provides a characterization of the development of neural representations with learning across time. The behavioral analyses provide helpful insight into the participants' learning. However, there were some aspects of the conceptual setup and the analyses that I found somewhat difficult to follow. It would also be helpful to provide clearer links between specific predictions and theories of hippocampal function.

We appreciate the Reviewer’s careful read of our manuscript and their thoughtful guidance for improvement, which we believe strengthened the revised product. We note that responses to a number of the Reviewer’s points were surfaced by the Editor as Essential revisions; as such, in a number of instances in the point-by-point below we direct the Reviewer to our responses above under the Essential revisions section.

General comment 1: The motivation in the Introduction builds on the assumption that global representations are dependent on local ones. However, I was not completely sure about the specific predictions or assumptions regarding integration vs. differentiation and their time course in the present experimental design. What would pattern similarity consistent with 'early evidence of global map learning' (p. 7) look like? Fig. 1D was somewhat difficult to understand. The 'state space' representation is only shown in Figure 1 while all subsequent analyses are averaged pairwise correlations. It would be helpful to spell out predictions as they relate to the similarity between same-route vs. different-route neural patterns.

We appreciate this feedback. An increase in pattern similarity across features that span tracks would indicate the linking of those features together. ‘Early evidence’ here describes the point in experience where participants had traversed local (within-track) paths but had yet to traverse across-tracks.

Figure 1D seeks to communicate the high-level conceptual point about how similarity (abstractly represented as state-space distance) may change in one of two directions as a function of experience.

General comment 2: The shared landmarks could be used by the participants to infer how the three tracks connected even before they were able to cross between them. It is possible that the more efficient navigators used an explicit encoding strategy to help them build a global map of the world. While I understand the authors' reasoning for excluding the shared landmarks (p. 13), it seems like it could be useful to run an analysis including them as well - one possibility is that they act as 'anchors' and drive the similarity between different tracks early on; another is that they act as 'boundaries' and repel the representations across routes. Assuming that participants crossed over at these landmarks, these seem like particularly salient aspects of the environment.

We agree that these shared landmarks play an important role in learning the global environment and guiding participants’ navigation. However, they also add confounding elements to the analyses; mainly, shared landmarks are located near multiple goal locations and associated with multiple tracks, and transition probabilities differ at shared landmarks because they have an increased number of neighboring landmarks and fractals. In the initial submission, shared landmarks were included in all analyses except (a) global distance models and (b) context models (which compare items located on the same vs different tracks).

With respect to (a) the global distance models, we ran these models while including shared landmarks and the results did not differ (see figure below and compare to Fig. 5 in the revised manuscript):

Distance representations in the Global Environment, with shared landmarks included. These data can be compared to Figure 5 of the revised manuscript, which does not include shared landmarks (see page 5 of this response letter).

We continue to report the results from models excluding shared landmarks due to the confounding factors described above, with the following addition to the Results section:

“We excluded shared landmarks from this model as they are common to multiple tracks; however, the results do not differ if these landmarks are included in the analysis.”

With respect to (b) the context analyses (which compare items located on the same vs different tracks), we cannot include shared landmarks in these analyses because they are common amongst multiple tracks and thus confound the analyses. Finally, we are unable to conduct additional analyses investigating shared landmarks specifically (for example, examining how similarity between shared landmarks evolves across learning) due to very low trial counts. We share the Reviewer’s perspective that the role of shared landmarks during the building of map representations promises to provide additional insights and believe this is a promising question for future investigation.

General comment 3: What were the predictions regarding the fractals vs. landmarks (p. 13)? It makes sense to compare like-to-like, but since both were included in the models it would be helpful to provide predictions regarding their similarity patterns.

We are grateful for the feedback on how to improve the consistency of results reporting. In the revision, we updated the relevant sections of the manuscript to include results from fractals. Please see our above response to Essential Revisions General comment #5 for additions made to the text.

General comment 4: The median split into less-efficient and more-efficient groups does not seem to be anticipated in the Introduction and results in a small-N group comparison. Instead, as the authors have a wealth of within-individual data, it might be helpful to model single-trial navigation data in relation to pairwise similarity values for each given pair of landmarks in a mixed-effects model. While there won't be a simple one-to-one mapping and fMRI data are noisy, this approach would afford higher statistical power due to more within-individual observations and would avoid splitting the sample into small subgroups.

We appreciate this very helpful suggestion. Following this guidance, we removed the median-split analysis and ran a mixed-effects model relating trial-wise navigation data (at the beginning of the Global Navigation Task) to pairwise similarity values for each given pair of landmarks and fractals (Post Local Navigation). We also altered our approach to the across-participant analysis examining brain-behavior relationships. Please see our above response to Essential Revisions General comment #3 for additions to the revised manuscript.

General comment 5: If I understood correctly, comparing Fig. 4B and Fig. 5B suggests that the relationship between higher link distance and lower representational similarity was driven by less efficient navigators. The performance on average improved over time to more or less the same level as within-track (Fig. 2). Were less efficient navigators particularly inefficient on trials with longer distances? In the context of models of hippocampal function, this suggests that good navigators represented all locations as equidistant while poorer navigators showed representations more consistent with a map - locations that were further apart were more distant in their representational patterns. Perhaps more fine-grained analyses linking neural patterns to behavior would be helpful here.

Following the above guidance, we removed the median-split analyses when exploring across-participant brain-behavior relationships (see Essential Revisions General comment #3), replacing it with a mixed-effects model analysis, and we revised our discussion of the across-track link distance effects (see Essential Revisions General comment #4). For this reason, we were hesitant and ultimately decided against conducting the proposed fine-grained analyses on the median-split data.

General comment 6: I'm not completely sure how to interpret the functional connectivity analysis between the vmPFC and the hippocampus vs. visual cortex (Fig. 6). The analysis shows that the hippocampus and visual cortex are generally more connected than the vmPFC and visual cortex - but this relationship does not show an experience-dependent relationship and is consistent with resting-state data where the hippocampus tends to cluster into the posterior DMN network.

We expected to see an experience-dependent relationship between vmPFC and hippocampal pattern similarity, and agree that these findings are difficult to interpret. Based on comments from several reviewers, we removed the second-order similarity analysis from the manuscript in favor of an analysis which models the relationship between vmPFC pattern similarity and hippocampal pattern similarity. Moreover, given the exploratory nature of the vmPFC analyses, and following guidance from Reviewer 1 about the visual cortex control analyses, both were moved to the Appendix. Please see our above response to Essential Revisions General comment #7 for further details of the changes made to the manuscript.

Reviewer #3 (Public Review):

Fernandez et al. report results from a multi-day fMRI experiment in which participants learned to locate fractal stimuli along three oval-shaped tracks. The results suggest the concurrent emergence of a local, differentiated within-track representation and a global, integrated cross-track representation. More specifically, the authors report decreases in pattern similarity for stimuli encountered on the same track in the entorhinal cortex and hippocampus relative to a pre-task baseline scan. Intriguingly, following navigation on the individual tracks, but prior to global navigation requiring track-switching, pattern similarity in the hippocampus correlated with link distances between landmark stimuli. This effect was only observed in participants who navigated less efficiently in the global navigation task and was absent after global navigation.

Overall, the study is of high quality in my view and addresses relevant questions regarding the differentiation and integration of memories and the formation of so-called cognitive maps. The results reported by the authors are interesting and are based upon a well-designed experiment and thorough data analysis using appropriate techniques. A more detailed assessment of strengths and weaknesses can be found below.

Strengths

1) The authors address an interesting question at the intersection of memory differentiation and integration. The study is further relevant for researchers interested in the question of how we form cognitive maps of space.

2) The study is well-designed. In particular, the pre-learning baseline scan and the random-order presentation of stimuli during MR scanning allow the authors to track the emergence of representations in a well-controlled fashion. Further, the authors include an adequate control region and report direct comparisons of their effects against the patterns observed in this control region.

3) The manuscript is well-written. The introduction provides a good overview of the research field and the discussion does a good job of summarizing the findings of the present study and positioning them in the literature.

We thank Dr. Bellmund for his positive evaluation of the manuscript. We greatly appreciate the insightful feedback, which we believe strengthened the manuscript’s clarity and potential impact. We note that responses to a number of Dr. Bellmund’s points were surfaced by the Editor as Essential revisions; as such, in a number of instances in the point-by-point below we direct the Reviewer to our responses above under the Essential revisions section.

Weaknesses

General comment 1: Despite these distinct strengths, the present study also has some weaknesses. On the behavioral level, I am wondering about the use of path inefficiency as a metric for global navigation performance. Because it is quantified based on the local response, it conflates the contributions of local and global errors.

We appreciate this point with respect to path inefficiency during global navigation. As noted below, following Dr. Bellmund’s further insightful guidance, we now complement the path inefficiency analyses with additional metrics of across-track (global) navigation performance, which effectively separate local from global errors (please see below response to Author recommendation #1).

General comment 2: For the distance-based analysis in the hippocampus, the authors choose to only analyze landmark images and do not include fractal stimuli. There seems to be little reason to expect that distances between the fractal stimuli, on which the memory task was based, would be represented differently relative to distances between the landmarks.

We are grateful for the feedback on how to improve the consistency of results reporting. In the revision, we updated the relevant sections of the manuscript to include results from fractals. Please see our above response to Essential Revisions General comment #5 for full details.

General comment 3: Related to the aforementioned analysis, I am wondering why the authors chose the link distance between landmarks as their distance metric for the analysis and why they limit their analysis to pairs of stimuli with distance 1 or 2 and do not include pairs separated by the highest possible distance (3).

We appreciate the request for clarification here. Beginning with the latter question, we note that the highest possible distance varies between within-track vs. across-track paths. If participants navigate in the Local Navigation Task using the shortest or most efficient path, the highest possible within-track link distance between two stimuli is 2. For this reason, the Local Navigation/within-track analysis includes link distances of 1 and 2. For the Global Navigation analysis, we also include pairs of stimuli with link distances of 3 and 4 when examining across-track landmarks.

Regarding the use of link distance as the distance metric, we note that the path distance (a.u.) varies only slightly between pairs of stimuli with the same link distance. As such, categorical treatment link distance accounts for the vast majority of the variance in path distance and thus is a suitable approach. Please note that in the new trial-level brain-behavior analysis included in the revised manuscript (which replaces the median-split analysis), we used the length of the optimal path.

General comment 4: Surprisingly, the authors report that across-track distances can be observed in the hippocampus after local navigation, but that this effect cannot be detected after global, cross-track navigation. Relatedly, the cross-track distance effect was detected only in the half of participants that performed relatively badly in the cross-track navigation task. In the results and discussion, the authors suggest that the effect of cross-track distances cannot be detected because participants formed a "more fully integrated global map". I do not find this a convincing explanation for why the effect the authors are testing would be absent after global navigation and for why the effect was only present in those participants who navigated less efficiently.

We appreciate Dr. Bellmund’s input here, which was shared by other reviewers. We revised and clarified the Discussion based on reviewer comments. Please see our above response to Essential Revisions General comment #4 for full details.

General comment 5: The authors report differences in the hippocampal representational similarity between participants who navigated along inefficient vs. efficient paths. These are based on a median split of the sample, resulting in a comparison of groups including 11 and 10 individuals, respectively. The median split (see e.g. MacCallum et al., Psychological Methods, 2002) and the low sample size mandate cautionary interpretation of the resulting findings about interindividual differences.

We appreciate the feedback we received from multiple reviewers with respect to the median-split brain-behavior analysis. We replaced the median-split analysis with the following: 1) a mixed-effects model predicting neural pattern similarity Post Local Navigation, with a continuous metric of task performance (each participant’s median path inefficiency for across-track trials in the first four test runs of Global Navigation) and link distance as predictors; and 2) a mixed-effects model relating trial-wise navigation data to pairwise similarity values for each given pair of landmarks and fractals (as suggested by Reviewer 2). Please see our above response to Essential Revisions General comment #3 for additions to the revised manuscript.

Author Response:

Evaluation Summary:

This manuscript is of primary interest to readers in the field of infectious diseases especially the ones involved in COVID-19 research. The identification of immunological signatures caused by SARS-CoV-2 in HIV-infected individuals is important not only to better predict disease outcomes but also to predict vaccine efficacy and to potentially identify sources of viral variants. In here, the authors leverage a combination of clinical parameters, limited virologic information and extensive flow cytometry data to reach descriptive conclusions.

We have extensively reworked the paper.

Reviewer #1 (Public Review):

The methods appear sound. The introduction of vaccines for COVID-19 and the emergence of variants in South Africa and how they may impact PLWH is well discussed making the findings presented a good reference backdrop for future assessment. Good literature review is also presented. Specific suggestions for improving the manuscript have been identified and conveyed to the authors.

We thank the Reviewer for the support.

Reviewer #2 (Public Review):

Karima, Gazy, Cele, Zungu, Krause et al. described the impact of HIV status on the immune cell dynamics in response to SARS-CoV-2 infection. To do so, during the peak of the KwaZulu-Natal pandemic, in July 2020, they enrolled a robust observational longitudinal cohort of 124 participants all positive for SARS-CoV-2. Of the participants, a group of 55 people (44%) were HIV-infected individuals. No difference is COVID-19 high risk comorbidities of clinical manifestations were observed in people living with HIV (PLWH) versus HIV-uninfected individuals exception made for joint ache which was more present in HIV-uninfected individuals. In this study, the authors leverage and combine extensive clinical information, virologic data and immune cells quantification by flow cytometry to show changes in T cells such as post-SARS-CoV-2 infection expansion of CD8 T cells and reduced expression CXCR3 on T cells in specific post-SARS-CoV-2 infection time points. The authors also conclude that the HIV status attenuates the expansion of antibody secreting cells. The correlative analyses in this study show that low CXCR3 expression on CD8 and CD4 T cells correlates with Covid-19 disease severity, especially in PLWH. The authors did not observe differences in SARS-CoV-2 shedding time frame in the two groups excluding that HIV serostatus plays a role in the emergency of SARS-CoV-2 variants. However, the authors clarify that their PLWH group consisted of mostly ART suppressed participants whose CD4 counts were reasonably high. The study presents the following strengths and limitations

We thank the Reviewer for the comments. The cohort now includes participants with low CD4.

Strengths:

A. A robust longitudinal observational cohort of 124 study participants, 55 of whom were people living with HIV. This cohort was enrolled in KwaZulu-Natal,South Africa during the peak of the pandemic. The participants were followed for up to 5 follow up visits and around 50% of the participants have completed the study.

We thank the Reviewer for the support. The cohort has now been expanded to 236 participants.

B. A broad characterization of blood circulating cell subsets by flow cytometry able to identify and characterize T cells, B cells and innate cells.

We thank the Reviewer for the support.

Weaknesses:

The study design does not include

A. a robust group of HIV-infected individuals with low CD4 counts, as also stated by the authors

This has changed in the resubmission because we included participants from the second, beta variant dominated infection wave. For this infection wave we obtained what we think is an important result, presented in a new Figure 2:

This figure shows that in infection wave 2 (beta variant), CD4 counts for PLWH dropped to below the CD4=200 level, yet recovered after SARS-CoV-2 clearance. Therefore, the participants we added had low CD4 counts, but this was SARS-CoV-2 dependent.

B. a group of HIV-uninfected individuals and PLWH with severe COVID-19. As stated in the manuscript the majority of our participants did not progress beyond outcome 4 of the WHO ordinal scale. This is also reflected in the age average of the participants. Limiting the number of participants characterized by severe COVID-19 limits the study to an observational correlative study

Death has now been added to Table 1 under the “Disease severity” subheading. The number of participants who have died, at 13, is relatively small. We did not limit the study to non-critical cases. Our main measure of severity is supplemental oxygen.

This is stated in the Results, line 106-108:

“Our cohort design did not specifically enroll critical SARS-CoV-2 cases. The requirement for supplemental oxygen, as opposed to death, was therefore our primary measure for disease severity.”

This is justified in the Discussion, lines 219-225:

“Our cohort may not be a typical 'hospitalized cohort' as the majority of participants did not require supplemental oxygen. We therefore cannot discern effects of HIV on critical SARS-CoV-2 cases since these numbers are too small in the cohort. However, focusing on lower disease severity enabled us to capture a broader range of outcomes which predominantly ranged from asymptomatic to supplemental oxygen, the latter being our main measure of more severe disease. Understanding this part of the disease spectrum is likely important, since it may indicate underlying changes in the immune response which could potentially affect long-term quality of life and response to vaccines.”

C. a control group enrolled at the same time of the study of HIV-uninfected and infected individuals.

This was not possible given constraints imposed on bringing non-SARS-CoV-2 infected participants into a hospital during a pandemic for research purposes. However, given that the study was longitudinal, we did track participants after convalescence. This gave us an approximation of participant baseline in the absence of SARS-CoV-2, for the same participants. Results are presented in Figure 2 above.

D. results that elucidate the mechanisms and functions of immune cells subsets in the contest of COVID-19.

We do not have functional assays.

Reviewer #3 (Public Review):

Karim et al have assembled a large cohort of PLWH with acute COVID-19 and well-matched controls. The main finding is that, despite similar clinical and viral (e.g., shedding) outcomes, the immune response to COVID-19 in PLWH differs from the immune response to COVID-19 in HIV uninfected individuals. More specifically, they find that viral loads are comparable between the groups at the time of diagnosis, and that the time to viral clearance (by PCR) is also similar between the two groups. They find that PLWH have higher proportions and also higher absolute number of CD8 cells in the 2-3 weeks after initial infection.

The authors do a wonderful job of clinically characterizing the research participants. I was most impressed by the attention to detail with respect to timing of viral diagnosis as it related to symptom onset and specimen collection. I was also impressed by the number of longitudinal samples included in this study.

We thank the Reviewer for the support.

Author Response

Reviewer #2 (Public Review):

Silberberg et al. present a series of cryo-EM structures of the ATP dependent bacterial potassium importer KdpFABC, a protein that is inhibited by phosphorylation under high environmental K+ conditions. The aim of the study was to sample the protein's conformational landscape under active, non-phosphorylated and inhibited, phosphorylated (Ser162) conditions.

Overall, the study presents 5 structures of phosphorylated wildtype protein (S162-P), 3 structures of phosphorylated 'dead' mutant (D307N, S162-P), and 2 structures of constitutively active, non-phosphorylatable protein (S162A).

The true novelty and strength of this work is that 8 of the presented structures were obtained either under "turnover" or at least 'native' conditions without ATP, ie in the absence of any non-physiological substrate analogues or stabilising inhibitors. The remaining 2 were obtained in the presence of orthovanadate.

Comparing the presented structures with previously published KdpFACB structures, there are 5 structural states that have not been reported before, namely an E1-P·ADP state, an E1-P tight state captured in the autoinhibited WT protein (with and without vanadate), and two different nucleotide-free 'apo' states and an E1·ATP early state.

Of these new states, the 'tight' states are of particular interest, because they appear to be 'off-cycle', dead end states. A novelty lies in the finding that this tight conformation can exist both in nucleotide-free E1 (as seen in the published first KdpFABC crystal structure), and also in the phosphorylated E1-P intermediate.

By EPR spectroscopy, the authors show that the nucleotide free 'tight' state readily converts into an active E1·ATP conformation when provided with nucleotide, leading to the conclusion that the E1-P·ADP state must be the true inhibitory species. This claim is supported by structural analysis supporting the hypothesis that the phosphorylation at Ser162 could stall the KdpB subunit in an E1P state unable to convert into E2P. This is further supported by the fact that the phosphorylated sample does not readily convert into an E2P state when exposed to vanadate, as would otherwise be expected.

The structures are of medium resolution (3.1 - 7.4 Å), but the key sites of nucleotide binding and/or phosphorylation are reasonably well supported by the EM maps, with one exception: in the 'E1·ATP early' state determined under turnover conditions, I find the map for the gamma phosphate of ATP not overly convincing, leaving the question whether this could instead be a product-inhibited, Mg-ADP bound E1 state resulting from an accumulation of MgADP under the turnover conditions used. Overall, the manuscript is well written and carefully phrased, and it presents interesting novel findings, which expand our knowledge about the conformational landscape and regulatory mechanisms of the P-type ATPase family.

We thank the reviewer for their comments and helpful insights. We have addressed the points as follows:

However in my opinion there are the following weaknesses in the current version of the manuscript:

1) A lack of quantification. The heart of this study is the comparison of the newly determined KdpFABC structures with previously published ones (of which there are already 10). Yet, there are no RMSD calculations to illustrate the magnitude of any structural deviations. Instead, the authors use phrases like 'similar but not identical to', 'has some similarities', 'virtually identical', 'significant differences'. This makes it very hard to appreciate the true level of novelty/deviation from known structures.

This is a very valid point and we thank the reviewers for bringing it up. To provide a better overview and appreciation of conformational similarities and significant differences we have calculated RMSDs between all available structures of KdpFABC. They are summarised in the new Table 1 – Table Supplement 2. We have included individual rmsd values, whenever applicable and relevant, in the respective sections in the text and figures. We note that the RMSDs were calculated only between the cytosolic domains (KdpB N,A,P domains) after superimposition of the full-length protein on KdpA, which is rigid across all conformations of KdpFABC (see description in material and methods lines 1184-1191 or the caption to Table 1 – Table Supplement 2). We opted to not indicate the RMSD calculated between the full-length proteins, as the largest part of the complex does not undergo large structural changes (see Figure 1 – Figure Supplement 1, the transmembrane region of KdpB as well as KdpA, KdpC and KdpF show relatively small to no rearrangements compared to the cytosolic domains), and would otherwise obscure the relevant RMSD differences discussed here.

Also the decrease in EPR peak height of the E1 apo tight state between phosphorylated and non-phosphorylated sample - a key piece of supporting data - is not quantified.

EPR distance distributions have been quantified by fitting and integrating a gaussian distribution curve, and have been added to the corresponding results section (lines 523-542) and the methods section (lines 1230-1232).

2) Perhaps as a consequence of the above, there seems to be a slight tendency towards overstatements regarding the novelty of the findings in the context of previous structural studies. The E1-P·ATP tight structure is extremely similar to the previously published crystal structure (5MRW), but it took me three reads through the paper and a structural superposition (overall RMSD less than 2Å), to realise that. While I do see that the existing differences, the two helix shifts in the P- and A- domains - are important and do probably permit the usage of the term 'novel conformation' (I don't think there is a clear consensus on what level of change defines a novel conformation), it could have been made more clear that the 'tight' arrangement of domains has actually been reported before, only it was not termed 'tight'.

As indicated above we have now included an extensive RMSD table between all available KdpFABC structures. To ensure a meaningful comparison, the rmsd are only calculated between the cytosolic domains after superimposition of the full-length protein on KdpA, as the transmembrane region of KdpFABC is largely rigid (see figure below panel B). However, we have to note that in the X-ray structure the transmembrane region of KdpB is displaced relative to the rest of the complex when compared to the arrangement found in any of the other 18 cryo-EM structures, which all align well in the TMD (see figure below panel C). These deviations make the crystal structure somewhat of an outlier and might be a consequence of the crystal packing (see figure below panel A). For completeness in our comparison with the X-Ray structure, we have included an RMSD calculated when superimposed on KdpA and additional RMSD that was calculated between structures when aligned on the TMD of KdpB (see figure below panel D,E). The reported RMSD that the reviewer mentiones of less than 2Å was probably obtained when superimposing the entire complex on each other (see figure below panel F). However, we do not believe that this is a reasonable comparison as the TMD of the complex is significantly displaced, which stands in strong contrast to all other RMSDs calculated between the rest of the structures where the TMD aligns well (see figure below panel B).

From the resulting comparisons, we conclude that the E1P-tight and the X-Ray structure do have a certain similarity but are not identical. In particular not in the relative orientation of the cytosolic domains to the rest of the complex. We hope that including the RMSD in the text and separately highlighting the important features of the E1P tight state in the section “E1P tight is the consequence of an impaired E1P/E2P transition“ makes the story now more conclusive.

Likewise, the authors claim that they have covered the entire conformational cycle with their 10 structures, but this is actually not correct, as there is no representative of an E2 state or functional E1P state after ADP release.

This is correct, and we have adjusted the phrasing to “close to the entire conformational cycle” or “the entire KdpFABC conformational cycle except the highly transient E1P state after ADP release and E2 state after dephosphorylation.”

3) A key hypothesis this paper suggests is that KdpFABC cannot undergo the transition from E1P tight to E2P and hence gets stuck in this dead end 'off cycle' state. To test this, the authors analysed an S162-P sample supplied with the E2P inducing inhibitor orthovanadate and found about 11% of particles in an E2P conformation. This is rationalised as a residual fraction of unphosphorylated, non-inhibited, protein in the sample, but the sample is not actually tested for residual unphosphorylated fraction or residual activity. Instead, there is a reference to Sweet et al, 2020. So the claim that the 11% E2P particles in the vanadate sample are irrelevant, whereas the 14% E1P tight from the turnover dataset are of key importance, would strongly benefit from some additional validation.

We have added an ATPase assay that shows the residual ATPase activity of WT KdpFABC compared to KdpFABS162AC, both purified from E. coli LB2003 cells, which is identical to the protein production and purification for the cryo-EM samples (see Figure 2-Suppl. Figure 5). The residual ATPase activity is ca. 14% of the uninhibited sample, which correlates with the E2-P fraction in the orthovanadate sample.

Reviewer #3 (Public Review):

The authors have determined a range of conformations of the high-affinity prokaryotic K+ uptake system KdpFABC, and demonstrate at least two novel states that shed further light on the structure and function of these elusive protein complexes.

The manuscript is well-written and easy to follow. The introduction puts the work in a proper context and highlights gaps in the field. I am however missing an overview of the currently available structures/states of KdpFABC. This could also be implemented in Fig. 6 (highlighting new vs available data). This is also connected to one of my main remarks - the lack of comparisons and RMSD estimates to available structures. Similarity/resemblance to available structures is indicated several times throughout the manuscript, but this is not quantified or shown in detail, and hence it is difficult for the reader to grasp how unique or alike the structures are. Linked to this, I am somewhat surprised by the lack of considerable changes within the TM domain and the overlapping connectivity of the K indicated in Table 1 - Figure Supplement 1. According to Fig. 6 the uptake pathway should be open in early E1 states, but not in E2 states, contrasting to the Table 1 - Figure Supplement 1, which show connectivity in all structures? Furthermore, the release pathway (to the inside) should be open in the E2-P conformation, but no release pathway is shown as K ions in any of the structures in Table 1 - Figure Supplement 1. Overall, it seems as if rather small shifts in-between the shown structures (are the structures changing from closed to inward-open)? Or is it only KdpA that is shown?

We thank the reviewer for their positive response and constructive criticisms. We have addressed these comments as follows:

1. The overview of the available structures has been implemented in Fig. 6, with the new structures from this study highlighted in bold.

2. RMSD values have been added to all comparisons, with a focus on the deviations of the cytosolic domains, which are most relevant to our conformational assignments and discussions.

3. To highlight the (comparatively small) changes in the TMD, we have expanded Table 1 - Figure Supplement 1 to include panels showing the outward-open half-channel in the E1 states with a constriction at the KdpA/KdpB interface and the inward-open half-channel in the E2 states. The largest observable rearrangements do however take place in the cytosolic domains. This is an absolute agreement with previous studies, which focused more on the transition occurring within the transmembrane region during the transport cycle (Stock et al, Nature Communication 2018; Silberberg et al, Nature Communication 2021; Sweet et al., PNAS 2021).

4. The ions observed in the intersubunit tunnel are all before the point at which the tunnel closes, explaining why there is no difference in this region between E1 and E2 structures. Moreover, as we discussed in our last publication (Silberberg, Corey, Hielkema et al., 2021, Nat. Comms.), the assignment of non-protein densities along the entire length of the tunnel is contentious and can only be certain in the selectivity filter of KdpA and the CBS of KdpB.

5. The release pathway from the CBS does not feature any defined K+ coordination sites, so ions are not expected to stay bound along this inward-open half-channel.

My second key remark concerns the "E1-P tight is the consequence of an impaired E1-P/E2-P transition" section, and the associated discussion, which is very interesting. I am not convinced though that the nucleotide and phosphate mimic-stabilized states (such as E1-P:ADP) represent the high-energy E1P state, as I believe is indicated in the text. Supportive of this, in SERCA, the shifts from the E1:ATP to the E1P:ADP structures are modest, while the following high-energy Ca-bound E1P and E2P states remain elusive (see Fig. 1 in PMID: 32219166, from 3N8G to 3BA6). Or maybe this is not what the authors claim, or the situation is different for KdpFABC? Associated, while I agree with the statement in rows 234-237 (that the authors likely have caught an off-cycle state), I wonder if the tight E1-P configuration could relate to the elusive high-energy states (although initially counter-intuitive as it has been caught in the structure)? The claims on rows 358-360 and 420-422 are not in conflict with such an idea, and the authors touch on this subject on rows 436-450. Can it be excluded that it is the proper elusive E1P state? If the state is related to the E1P conformation it may well have bearing also on other P-type ATPases and this could be expanded upon.

This a good point, particularly since the E1P·ADP state is the most populated state in our sample, which is also counterintuitive to “high-energy unstable state”. One possible explanation is that this state already has some of the E1-P strains (which we can see in the clash of D307-P with D518/D522), but the ADP and its associated Mg2+ in particular help to stabilize this. Once ADP dissociates and takes the Mg2+ with it, the full destabilization takes effect in the actual high-energy E1P state. Nonetheless, we consider it fair to compare the E1P tight with the E1P·ADP to look for electrostatic relaxation. We have clarified the sequence of events and our hypothesized role the ADP/Mg2+ have in stabilizing the E1P·ADP state that we can see (lines 609-619): “Moreover, a comparison of the E1P tight structure with the E1P·ADP structure, its most immediate precursor in the conformational cycle obtained, reveals a number of significant rearrangements within the P domain (Figure 5B,C). First, Helix 6 (KdpB538-545) is partially unwound and has moved away from helix 5 towards the A domain, alongside the tilting of helix 4 of the A domain (Figure 5B,C – arrow 2). Second, and of particular interest, are the additional local changes that occur in the immediate vicinity of the phosphorylated KdpBD307. In the E1P·ADP structure, the catalytic aspartyl phosphate, located in the D307KTG signature motif, points towards the negatively charged KdpBD518/D522. This strain is likely to become even more unfavorable once ADP dissociates in the E1P state, as the Mg2+ associated with the ADP partially shields these clashes. The ensuing repulsion might serve as a driving force for the system to relax into the E2 state in the catalytic cycle.”

We believe it is highly unlikely that the reported E1-P tight state represents an on-cycle high-energy E1P intermediate. For one, we observe a relaxation of electrostatic strains in this structure, in particular when compared to the obtained E1P ADP state. By contrast, the E1P should be the most energetically unfavourable state possible to ensure the rapid transition to the E2P state. As such, this state should be a transient state, making it less likely to be obtainable structurally as an accumulated state. Additionally, the association of the N domain with the A domain in the tight conformation, which would have to be reverted, would be a surprising intermediary step in the transition from E1P to E2P. Altogether, the here reported E1P tight state most likely represents an off-cycle state.

Author Response:

Reviewer #1 (Public Review):

This manuscript was well written and interrogates an exciting and important question about whether thalamic sub-regions serve as essential "hubs" for interconnecting diverse cognitive processes. This lesion dataset, combined with normative imaging analyses, serves as a fairly unique and powerful way to address this question.

Overall, I found the data analysis and processing to be appropriate. I have a few additional questions that remain to be answered to strengthen the conclusions of the authors.

1. The number of cases of thalamic lesions was small (20 participants) and the sites of overlap in this group is at maximum 5 cases. Finding focal thalamic lesions with the appropriate characteristics is likely to be relatively hard, so this smaller sample size is not surprising, but it suggests that the overlap analyses conducted to identify "multi-domain" hub sites will be relatively underpowered. Given these considerations, I was a bit surprised that the authors did not start with a more hypothesis driven approach (i.e., separating the groups into those with damage to hubs vs. non-hubs) rather than using this more exploratory overlap analysis. It is particularly concerning that the primary "multi-domain" overlap site is also the primary site of overlap in general across thalamic lesion cases (Fig. 2A).

An issue that arises when attempting to separate lesions into “hub” versus “non-hub” lesions at the study onset is there is not an accepted definition or threshold for a binary categorization of hubs. The primary metric for estimating hub property, participation coefficient (PC), is a continuous measure ranging from 0 to 1, without an objective threshold to differentiate hub versus non-hub regions. Thus, a binary classification would require exploring an arbitrary threshold for splitting our sample. Our concern is that assigning an arbitrary threshold and delineating groups based on that threshold would be equally, if not more, exploratory. However, we appreciate this comment and future studies may be able to use the results of the current analysis to formulate an a priori threshold based on our current results. Similarly, given the relative difficulty recruiting patients with focal thalamic lesions, we did not have enough power to do a linear regression testing the relationship between PC and the global deficit score. Weighing all these factors, we determined that counting the number of tests impaired, and defining global deficit as more than one domain impaired, is a more objective and less exploratory approach for addressing our specific hypotheses than arbitrarily splitting PC values.

We agree with the reviewer that our unequal lesion coverage in the thalamus is a limitation. We have acknowledged this in the discussion section (line 561). There may very likely be other integrative sites (for example the medial pulvinar) that we missed simply because we did not have sufficient lesion coverage. We have updated our discussion section (line 561) to more explicitly discuss the limitation of our study.

1. Many of the comparison lesion sites (Fig. 1A) appear to target white matter rather than grey matter locations. Given that white matter damage may have systematically different consequences as grey matter damage, it may be important to control for these characteristics.

We have conducted further analyses to better control for the effects of white matter damage.

1. The use of cortical lesion locations as generic controls was a bit puzzling to me, as there are hub locations in the cortex as well as in the thalamus. It would be useful to determine whether hub locations in the cortex and thalamus show similar properties, and that an overlap approach such as the one utilized here, is effective at identifying hubs in the cortex given the larger size of this group.

We have conducted additional analyses to replicate our findings and validate our approach in a group of 145 expanded comparison patients. We found that comparison patients with lesions to brain regions with higher PC values exhibited more global deficits, when compared to patients that did not exhibit global deficits. Results from this additional analysis were included in Figure 6.

1. While I think the current findings are very intriguing, I think the results would be further strengthened if the authors were able to confirm: (1) that the multi-domain thalamic lesions are not more likely to impact multiple nuclei or borders between nuclei (this could also lead to a multi-domain profile of results) and (2) that the locations of these locations are consistent in their network functions across individuals (perhaps through comparisons with Greene et al., 2020 or more extended analyses of the datasets included in this work) as this would strengthen the connection between the individual lesion cases and the normative sample analyses.

We can confirm that multi-domain thalamic lesions did not cover more thalamic subdivisions (anatomical nuclei or functional parcellations). We also examined whether the multi-domain lesion site consistently showed high PC values in individual normative subjects. We calculated thalamic PC values for each of the 235 normative subjects, and compared the average PC values in the multi-domain lesion site versus the single domain-lesion site across these normative subjects. We found the multi-domain site exhibited significantly higher PC values (Figure 5D, t(234) = 6.472, p < 0.001). This suggest that the multi-domain lesion site consistently showed stronger connector hub property across individual normative subjects.

We also visually compared our results with Greene et al., 2020 (see below). We found that in the dorsal thalamus (z >10), there was a good spatial overlap between the integration zone reported in Greene et al 2020 and the multi-domain lesion site that we identified. In the ventral thalamus (z < 4), we did not identify the posterior thalamus as part of the multi-domain lesion site, likely because we did not have sufficient lesion coverage in the posterior thalamus.

In terms of describing the putative network functions of the thalamic lesion sites, results presented in Figure 7A indicate that multi-domain lesion sites in the thalamus were broadly coupled with cortical functional networks previously implicated in domain-general control processes, such as the cingulo-opercular network, the fronto-parietal network, and the dorsal attention network.

Greene, Deanna J., et al. "Integrative and network-specific connectivity of the basal ganglia and thalamus defined in individuals." Neuron 105.4 (2020): 742-758.

Author Response

Reviewer #1 (Public Review):

This study investigates low-frequency (LF) local field potentials and high-frequency (HF, >30 Hz) broadband activity in response to the visual presentation of faces. To this end, rhythmic visual stimuli were presented to 121 human participants undergoing depth electrode recordings for epilepsy. Recordings were obtained from the ventral occipito-temporal cortex and brain activity was analyzed using a frequency-tagging approach. The results show that the spatial, functional, and timing properties of LF and HF responses are largely similar, which in part contradicts previous investigations in smaller groups of participants. Together, these findings provide novel and convincing insights into the properties and functional significance of LF and HF brain responses to sensory stimuli.

Strengths

• The properties and functional significance of LF and HF brain responses is a timely and relevant basic science topic.

• The study includes intracranial recordings in a uniquely high number of human participants.

• Using a frequency tagging paradigm for recording and comparing LF and HF responses is innovative and straightforward.

• The manuscript is well-written and well-illustrated, and the interpretation of the findings is mostly appropriate.

Weaknesses

• The writing style of the manuscript sometimes reflects a "race" between the functional significance of LF and HF brain responses and researchers focusing on one or the other. A more neutral and balanced writing style might be more appropriate.

We would like first to thank the reviewer for his/her positive evaluation as well as constructive and helpful comments for revising our manuscript.

Regarding the writing style: we had one major goal in this study, which is to investigate the relationship between low and high frequencies. However, it is fair to say – as we indicate in our introduction section – that low frequency responses are increasingly cast aside in the intracranial recording literature. That is, an increasing proportion of publications simply disregard the evoked electrophysiological response that occur at the low end of the frequency spectrum, to focus exclusively on the high-frequency response (e.g., Crone et al., 2001; Flinker et al., 2011; Mesgarani and Chang, 2012; Bastin et al., 2013; Davidesco et al., 2013; Kadipasoaglu et al., 2016; 2017; Shum et al., 2013; Golan et al., 2016; 2017; Grossman et al., 2019; Wang et al., 2021, see list of references at the end of the reply).

Thus, on top of the direct objective comparison between the two types of signals that our study originally provides, we think that it is fair to somehow reestablish the functional significance of low frequency activity in intracranial recording studies.

The writing style reflects that perspective rather than a race between the functional significance of LF and HF brain responses.

• It remains unclear whether and how the current findings generalize to the processing of other sensory stimuli and paradigms. Rhythmic presentation of visual stimuli at 6 Hz with face stimuli every five stimuli (1.2 Hz) represents a very particular type of sensory stimulation. Stimulation with other stimuli, or at other frequencies likely induce different responses. This important limitation should be appropriately acknowledged in the manuscript.

We agree with the Reviewer 1 (see also Reviewer 2) that it is indeed important to discuss whether the current findings generalize to the other brain functions and to previous findings obtained with different methodologies. We argue that our original methodological approach allows maximizing the generalizability of our findings.

First, frequency-tagging approach is a longstanding stimulation method, starting from the 1930s (i.e., well before standard evoked potential recording methods; Adrian & Matthews, 1934; intracranially: Kamp et al., 1960) and widely used in vison science (Regan, 1989; Norcia et al., 2015) but also in other domains (e.g., auditory, somato-sensory stimulation). More importantly, this approach does not only significantly increase the signal-to-noise ratio of neural responses, but the objectivity and the reliability of the LF-HF signal comparison (objective identification and quantification of the responses, very similar analysis pipelines).

Second, regarding the frequency of stimulation, our scalp EEG studies with high-level stimuli (generally faces) have shown that the frequency selection has little effect on the amplitude and the shape of the responses, as long as the frequency is chosen within a suitable range for the studied function (Alonso-Prieto et al., 2013). Regarding the paradigm used specifically in the present study (originally reported in Rossion et al., 2015 and discussed in detail for iEEG studies in Rossion et al., 2018), it has been validated with a wide range of approaches (EEG, MEG, iEEG, fMRI) and populations (healthy adults, patients, children and infants), identifying typically lateralized occipito-temporal face-selective neural activity with a peak in the middle section of the lateral fusiform gyrus (Jonas et al., 2016; Hagen et al., 2020 in iEEG; Gao et al., 2018 in fMRI).

Importantly, specifically for the paradigm used in the present study, our experiments have shown that the neural face-selective responses are strictly identical whether the faces are inserted at periodic or non-periodic intervals within the train of nonface objects (Quek & Rossion, 2017), that the ratio of periodicity for faces vs. objects (e.g., 1/5, 1/7 … 1/11) does not matter as long as the face-selective responses do not overlap in time (Retter & Rossion, 2016; Retter et al., 2020) and that the responses are identical across a suitable range of base frequency rates (Retter et al., 2020).

Finally, we fully acknowledge that the category-selective responses would be different in amplitude and localization for other types of stimuli, as also shown in our previous EEG (Jacques et al., 2016) and iEEG (Hagen et al., 2020) studies. Yet, as indicated in our introduction and discussion section, there are many advantages of using such a highly familiar and salient stimulus as faces, and in the visual domain at least we are confident that our conclusions regarding the relationship between low and high frequencies would generalize to other categories of stimuli.

We added a new section on the generalizability of our findings at the end of the Discussion, p.32-33 (line 880) (see also Reviewer 2’s comments). Please see above in the “essential revisions” for the full added section.

Reviewer #2 (Public Review):

The study by Jacques and colleagues examines two types of signals obtained from human intracortical electroencephalography (iEEG) measures, the steady-state visual evoked potential and a broadband response extending to higher frequencies (>100 Hz). The study is much larger than typical for iEEG, with 121 subjects and ~8,000 recording sites. The main purpose of the study is to compare the two signals in terms of spatial specificity and stimulus tuning (here, to images of faces vs other kinds of images).

The experiments consisted of subjects viewing images presented 6 times per second, with every 5th image depicting a face. Thus the stimulus frequency is 6 Hz and the face image frequency is 1.2 Hz. The main measures of interest are the responses at 1.2 Hz and harmonics, which indicate face selectivity (a different response to the face images than the other images). To compare the two types of signals (evoked potential and broadband), the authors measure either the voltage fluctuations at 1.2 Hz and harmonics (steady-state visually evoked potential) or the fluctuations of broadband power at these same frequencies.

Much prior work has led to the interpretation of the broadband signal as the best iEEG correlate of spatially local neuronal activity, with some studies even linking the high-frequency broadband signal to the local firing rate of neurons near the electrode. In contrast, the evoked potential is often thought to arise from synchronous neural activity spread over a relatively large spatial extent. As such, the broadband signal, particularly in higher frequencies (here, 30-160 Hz) is often believed to carry more specific information about brain responses, both in terms of spatial fidelity to the cortical sources (the cortical point spread function) and in terms of functional tuning (e.g., preference for one stimulus class over another). This study challenges these claims, particularly, the first one, and concludes that (1) the point spread functions of the two signals are nearly identical, (2) the cortical locations giving rise to the two signals are nearly identical, and (3) the evoked potential has a considerably higher signal-to-noise ratio.

These conclusions are surprising, particularly the first one (same point spread functions) given the literature which seems to have mostly concluded that the broadband signal is more local. As such, the findings pose a challenge to the field in interpreting the neuronal basis of the various iEEG signals. The study is large and well done, and the analysis and visualizations are generally clear and convincing. The similarity in cortical localization (which brain areas give rise to face-selective signals) and in point-spread functions are especially clear and convincing.

We thank the reviewer for his/her fair and positive evaluation of our work and helpful comments.

Although the reviewer does not disagree or criticize our methodology, we would like to reply to their comment about the surprising nature of our findings (particularly the similar spatial extent of LF and HF). In fact, we think that there is little evidence for a difference in ‘point-spread’ function in the literature, and thus that these results are not really that surprising. As we indicate in the original submission (discussion), in human studies, to our knowledge, the only direct comparisons of spatial extent of LF responses and HF is performed by counting and reporting the number of significant electrodes showing a significant response in the two signals (Miller et al., 2007; Crone et al., 1998; Pfurtscheller et al., 2003; see list of references at the end of the reply). Overall, these studies find a smaller number of significant electrodes with HF compared to LF. Intracranial EEG studies pointing to a more focal origin of HF activity generally cite one or several of these publications (e.g. Shum et al., 2013). In the current study, we replicate this finding and provide additional analyses showing that it is confounded with SNR differences across signals and created artificially by the statistical threshold. When no threshold is used and a more appropriate measure of spatial extent is computed (here, spatial extent at half maximum), we find no difference between the 2 signals, except for a small difference in the left anterior temporal lobe. Moreover, in intracranial EEG literature, the localness of the HF response is often backed by the hypothesis that HF is a proxy for firing rate. Indeed, since spikes are supposed to be local, it is implied that HF has to be local as well. However, while clear correlations have been found between HF measured with micro-electrodes and firing rate (e.g., Nir et al. 2007; Manning et al., 2009), there is no information on how local the activity measured at these electrodes is, and no evidence that the HF signal is more local than LF signal in these recordings. Last, the link between (local?) firing rate and HF/broadband signal has been show using micro-electrodes which vastly differ in size compared to macro-electrodes. The nature of the relationship and its spatial properties may differ between micro-electrodes and macro-electrodes used in ECOG/SEEG recordings.

We feel these points were all already discussed thoroughly in the original submission of the manuscript (see p. 28-30 in the revised manuscript) and did not modify the revised manuscript.

The lack of difference between the two signals (other than SNR), might ordinarily raise suspicion that there is some kind of confound, meaning that the two measures are not independent. Yet there are no obvious confounds: in principle, the broadband measure could reflect the high-frequency portion of the evoked response, rather than a separate, non-phase locked response to the signal. However, this is unlikely, given the rapid fall-off in the SSVEP at amplitudes much lower than the 30 Hz low-frequency end of the broadband measure. And the lack of difference between the two signals should not be confused for a null result: both signals are robust and reliable, and both are largely found in the expected parts of the brain for face selectivity (meaning the authors did not fail to measure the signals - it just turns out that the two measures have highly similar characteristics).

The current reviewer and reviewer #3 both commented or raised concerned about the fact that HF signal as measured in our study might be contaminated by LF evoked response, thereby explaining our findings of a strong similarity between the 2 signals.

This was actually a potential (minor) concern given the time-frequency (wavelet) parameters used in the original manuscript. Indeed, the frequency bandwidth (as measured as half width at half maximum) of the wavelet used at the lower bound (30Hz) of the HF signal extended to 11Hz (i.e., half width at half maximum = 19 Hz). At 40Hz, the bandwidth extended to 24Hz (i.e., HWHM = 16 Hz). While low-frequency face-selective responses at that range (above 16 Hz) are negligible (see e.g., Retter & Rossion, 2016; and data below for the present study), they could have potentially slightly contaminated the high frequency activity indeed.

To fully ensure that our findings could not be explained by such a contamination, we recomputed the HF signal using wavelets with a smaller frequency bandwidth and changed the high frequency range to 40-160 Hz. This ensures that the lowest frequency included in the HF signal (defined as the bottom of the frequency range minus half of the frequency bandwidth, i.e., half width at half maximum) is 30 Hz, which is well above the highest significant harmonic of face-selective response in our frequency-tagging experiment (i.e., 22.8 Hz ; defined as the harmonic of face frequency where, at group level, the number of recording contacts with a significant response was not higher than the number of significant contacts detected for noise in bins surrounding harmonics of the face frequency, see figure below). Thus, the signal measured in the 40-160 Hz range is not contaminated by lower frequency evoked responses.

We recomputed all analyses and statistics as reported in the original manuscript with the new HF definition. Overall, this change had very little impact on the findings, except for slightly lower correlation between HF and LF (in Occipital and Anterior temporal lobe) when using single recording contacts as unit data points (Note that we slightly modified the way we compute the maximal expected correlation. Originally we used the test-retest reliability averaged over LF and HF; in the revised version we use the lower reliability value of the 2 signals, which is more correct since the lower reliability is the true upper limit of the correlation). This indicates that the HF activity was mostly independent from phase-locked LF signal already in the original submission. However, since the analyses with the revised time-frequency analyses parameters enforce this independence, the revised analyses are reported as the main analyses in the manuscript.

The manuscript was completely revised accordingly and all figures (main and supplementary) were modified to reflect these new analyses. We also extended the methods section on HF analyses (p. 37) to indicate that HF parameters were selected to ensure independence of the HF signal from the LF evoked response, and provide additional information on wavelet frequency bandwidth.

There are some limitations to the possible generalizability of the conclusions drawn here. First, all of the experiments are of the same type (steady-state paradigm). It could be that with a different experimental design (e.g., slower and/or jittered presentation) the results would differ. In particular, the regularity of the stimulation (6 Hz images, 1.2 Hz faces) might cause the cortex to enter a rhythmic and non-typical state, with more correlated responses across signal types. Nonetheless, the steady-state paradigm is widely used in research, and even if the conclusions turn out to hold only for this paradigm, they would be important. (And of course, they might generalize beyond it.)

We understand the concern of the reviewer and appreciate the last statement about the wide use of the steady-state paradigm and the importance of our conclusions. Above that, we are very confident that our results can be generalized to slower and jittered presentations. Indeed, with this paradigm in particular, we have compared different frequency rates and periodic and nonperiodic stimulations in previous studies (Retter & Rossion, 2016; Quek et al., 2017; Retter et al., 2020). Importantly, specifically for the paradigm used in the present study, the neural face-selective responses are strictly identical whether the faces are inserted at periodic or non-periodic intervals within the train of nonface objects (Quek & Rossion, 2017), showing that the regularity of stimulation does not cause a non-typical state.

Please see our reply above to essential revisions and reviewer 1, in which we fully address this issue, as well as the revised discussion section (p. 32-33).

A second limitation is the type of stimulus and neural responses - images of faces, face-selectivity of neural responses. If the differences from previous work on these types of signals are due to the type of experiment - e.g., finger movements and motor cortex, spatial summation and visual cortex - rather than to the difference in sample size of type of analysis, then the conclusions about the similarity of the two types of signals would be more constrained. Again, this is not a flaw in the study, but rather a possible limitation in the generality of the conclusions.

This is a good point, which has been discussed above also. Please note that this was already partly discussed in the original manuscript when discussing the potential factors explaining the spatial differences between our study and motor cortex studies:

“Second, the hypothesis for a more focal HF compared to LF signals is mostly supported by recordings performed in a single region, the sensorimotor cortex (Miller et al., 2007; Crone et al., 1998; Pfurtscheller et al., 2003; Hermes et al., 2012), which largely consist of primary cortices. In contrast, here we recorded across a very large cortical region, the VOTC, composed of many different areas with various cortical geometries and cytoarchitectonic properties. Moreover, by recording higher-order category-selective activity, we measured activity confined to associative areas. Both neuronal density (Collins et al., 2010; Turner et al., 2016) and myelination (Bryant and Preuss, 2018) are substantially lower in associative cortices than in primary cortices in primates, and these factors may thus contribute to the lack of spatial extent difference between HF and LF observed here as compared to previous reports.” (p. 29-30).

Also in the same section (p. 30) we refer to the type of signals compared in previous motor cortex studies:

“Third, previous studies compared the spatial properties of an increase (relative to baseline) in HF amplitude to the spatial properties of a decrease (i.e. event-related desynchronization) of LF amplitude in the alpha and beta frequency ranges (Crone et al.,1998; 2001; Pfurtscheller et al., 2003; Miller et al., 2007; Hermes et al., 2012). This comparison may be unwarranted due to likely different mechanisms, brain networks and cortical layers involved in generating neuronal increases and decreases (e.g., input vs. modulatory signal, Pfurtscheller and Lopes da Silva, 1999; Schroeder and Lakatos, 2009). In the current study, our frequency-domain analysis makes no assumption about the increase and decrease of signals by face relative to non-face stimuli.”

In the original submission, we also acknowledged that the functional correspondence between LF and HF signals is not at ceiling (p. 31) :

“We acknowledge that the correlations found here are not at ceiling and that there were also slight offsets in the location of maximum amplitude across signals along electrode arrays (Figures 5 and 6). This lack of a complete functional overlap between LF and HF is also in line with previous reports of slightly different selectivity and functional properties across these signals, such as a different sensitivity to spatial summation (Winawer et al., 2013), to selective attention (Davidesko et al., 2013) or to stimulus repetition (Privmann et al., 2011). While part of these differences may be due to methodological differences in signal quantification, they also underline that these signals are not always strongly related, due to several factors. For instance, although both signals involve post-synaptic (i.e., dentritic) neural events, they nevertheless have distinct neurophysiological origins (that are not yet fully understood; see Buszaki, 2012; Leszczyński et al., 2020; Miller et al., 2009). In addition, these differing neurophysiological origins may interact with the precise setting of the recording sites capturing these signals (e.g., geometry/orientation of the neural sources relative to the recording site, cortical depth in which the signals are measured).”

Additional arguments regarding the generalizability can be found in the added section of the discussion as mentioned above.

Finally, the study relies on depth electrodes, which differs from some prior work on broadband signals using surface electrodes. Depth electrodes (stereotactic EEG) are in quite wide use so this too is not a criticism of the methods. Nonetheless, an important question is the degree to which the conclusions generalize, and surface electrodes, which tend to have higher SNR for broadband measures, might, in principle, show a different pattern than that observed her.

This is an interesting point, which cannot be addressed in our study obviously. We agree with the reviewer’s point. However, in contrast to ECoG, which is restricted to superficial cortical layers and gyri, SEEG has the advantages of sampling all cortical layers and a wide range anatomical structures (gyri, sulci, deep structures as medial temporal structures. Therefore, we believe that using SEEG ensures maximal generalizability of our findings. Overall, the relatively low spatial resolution of these 2 recording methods (i.e., several millimeters) compared the average cortical thickness (~2-3 mm) makes it very unlikely that SEEG and ECOG would reveal different patterns of LF-HF functional correspondence.

We added this point in a new section on the generalizability of our findings at the end of the Discussion (p.33, line 896).

Overall, the large study and elegant approach have led to some provocative conclusions that will likely challenge near-consensus views in the field. It is an important step forward in the quantitate analysis of human neuroscience measurements.

We sincerely thank the reviewer for his/her appreciation of our work

Reviewer #3 (Public Review):

Jacques et al. aim to assess properties of low and high-frequency signal content in intracranial stereo encephalography data in the human associative cortex using a frequency tagging paradigm using face stimuli. In the results, a high correspondence between high- and low-frequency content in terms of concordant dynamics is highlighted. The major critique is that the assessment in the way it was performed is not valid to disambiguate neural dynamics of responses in low- and high-frequency frequency bands and to make general claims about their selectivity and interplay.

The periodic visual stimulation induces a sharp non-sinusoidal transient impulse response with power across all frequencies (see Fig. 1D time-frequency representation). The calculated mean high-frequency amplitude envelope will therefore be dependent on properties of the used time-frequency calculation as well as noise level (e.g. 1/f contributions) in the chosen frequency band, but it will not reflect intrinsic high-frequency physiology or dynamics as it reflects spectral leakage of the transient response amplitude envelope. For instance, one can generate a synthetic non-sinusoidal signal (e.g., as a sum of sine + a number of harmonics) and apply the processing pipeline to generate the LF and HF components as illustrated in Fig. 1. This will yield two signals which will be highly similar regardless of how the LF component manifests. The fact that the two low and high-frequency measures closely track each other in spatial specificity and amplitudes/onset times and selectivity is due to the fact that they reflect exactly the same signal content. It is not possible with the measures as they have been calculated here to disambiguate physiological low- and high-frequency responses in a general way, e.g., in the absence of such a strong input drive.

The reviewer expresses strong concerns that our measure of HF activity is merely a reflection of spectral leakage from (lower-frequencies) evoked responses. In other words, physiological HF activity would not exist in our dataset and would be artificially created by our analyses. We should start by mentioning that this comment is in no way specific to our study, but could in fact be directed at all electrophysiological studies measuring stimulus-driven responses in higher frequency bands.

Reviewer 2 also commented on the possible contamination of evoked response in HF signal.

This was actually a potential (minor) concern given the time-frequency (wavelet) parameters used in the original manuscript. Indeed, the frequency bandwidth (as measured as half width at half maximum) of the wavelet used at the lower bound (30Hz) of the HF signal extended to 11Hz (i.e., half width at half maximum = 19 Hz). At 40Hz, the bandwidth extended to 24Hz (i.e., HWHM = 16 Hz). While low-frequency face-selective responses at that range (above 16 Hz) are negligible (see e.g., Retter & Rossion, 2016; and data below for the present study), they could have potentially slightly contaminated the high frequency activity indeed.

To ensure that our findings cannot be explained by such a contamination, we recomputed the HF signal using wavelet with a smaller frequency bandwidth and changed the frequency range to 40-160Hz. This ensures that the lowest frequency included in the HF signal (defined as the bottom of the frequency range minus half of the frequency bandwidth, i.e., half width at half maximum) was 30 Hz. This was well above the highest significant harmonic of face-selective response in our FPVS experiment which was 22.8 Hz (defined as the harmonic of face frequency where, at group level, the number of recording contacts with a significant response was not higher than the number of significant contacts detected for noise in bins surrounding harmonics of the face frequency, see figure below). This ensures that the signal measured in the 40-160Hz range is not contaminated by lower frequency evoked responses.

We recomputed all analyses and statistics from the manuscript with the new HF definition. Overall, this change had very little impact on the findings, except for slightly lower correlation between HF and LF (in Occipital and Anterior temporal lobe) when using single recording contacts as unit data points (Note that we slightly modified the way we compute the maximal expected correlation. Originally we used the test-retest reliability averaged over LF and HF; now we use the lower reliability value of the 2 signals, which is more correct since the lower reliability is the true upper limit of the correlation) This indicates that the HF activity was mostly independent from phase-locked LF signal already in the original submission. However, since the analyses with the revised time-frequency analyses parameters enforces this independence, we choose to keep the revised analyses as the main analyses in the manuscript.

The manuscript was completely revised accordingly and all figures (main and supplementary) were modified to reflect the new analyses. We also extended the method section on HF analyses (p. 37) to indicate that HF parameters were selected to ensure independence of the HF signal from the LF evoked response, and provide additional information on wavelet frequency bandwidth.

We believe our change in the time-frequency parameters and frequency range (40-160 Hz), the supplementary analyses using 80-160 Hz signal (per request of reviewer #2; see Figure 5 – figure supplement 4 and 5) and the fact that harmonics of the face frequency signal are not observed beyond ~23Hz, provide sufficient assurances that our findings are not driven by a contamination of HF signal by evoked/LF responses (i.e., spectral leakage).

With respect to the comment of the reviewer on the 1/f contributions on frequency band computation, as indicated in the original manuscript, the HF amplitude envelope is converted to percent signal change, separately for each frequency bin over the HF frequency range, BEFORE averaging across frequency bands. This steps works as a normalization step to remove the 1/f bias and ensures that each frequency in the HF range contributes equally to the computed HF signal. This was added to the method section (HF analysis, p 38 (line 1038) ): ” This normalization step ensures that each frequency in the HF range contributes equally to the computed HF signal, despite the overall 1/f relationship between amplitude and frequency in EEG.”

The connection of the calculated measures to ERPs for the low-frequency and population activity for the high-frequency measures for their frequency tagging paradigm is not clear and not validated, but throughout the text they are equated, starting from the introduction.

The frequency-tagging approach is widely used in the electrophysiology literature (Norcia et al., 2015) and as such requires no further validation. In the case our particular design, the connection between frequency-domain and time-domain representation for low-frequencies has been shown in numerous of our publications with scalp EEG (Rossion et al., 2015; Jacques et al., 2016; Retter and Rossion, 2016; Retter et al., 2020). FPVS sequences can be segmented around the presentation of the face image (just like in a traditional ERP experiment) and averaged in the time-domain to reveal ERPs (e.g., Jacques et al., 2016; Retter and Rossion, 2016; Retter et al., 2020). Face-selectivity of these ERPs can be isolated by selectively removing the base rate frequencies through notch-filtering (e.g., Retter and Rossion, 2016; Retter et al., 2020). Further, we have shown that the face-selective ERPs generated in such sequences are independent of the periodicity, or temporal predictability, of the face appearance (Queck et al. 2017) and to a large extent to the frequency of face presentation (i.e., unless faces are presented too close to each other, i.e., below 400 ms interval; Retter and Rossion, 2016). The high frequency signal in our study is measured in the same manner as in other studies and we simply quantify the periodic amplitude modulation of the HF signal. HF responses in frequency-tagging paradigm has been measured before (e.g., Winawer et al., 2013). In the current manuscript, Figure 1 provides a rational and explanation of the methodology. We also think that our manuscript in itself provides a form of validation for the quantification of HF signal in our particular frequency-tagging setup.

Author Response:

Reviewer #1 (Public Review):

Kursel et al. examined the evolution of synaptonemal complex proteins in C.elegans. While the sequence of the SC proteins evolved rapidly analysis of the structure of SC central region proteins from Caenorhabditis, Drosophila and mammalian species revealed that the length and placement of the coiled-coil domains, as well as overall protein length, were highly conserved across species. This conservation in the structure of coiled-coil proteins within the SC led to the proposal that the conserved structural parameters of the SC proteins and their coiled-coil domains could be used to identify central region components of the SC in species where components could not be identified on sequence conservation alone. Kursel et al demonstrated their parameters could be used to identify a transverse filament protein of the SC in the organism Pristionchus pacificus.

Due to high sequence divergence identifying SC proteins in new model systems has been challenging. The identification by Kursel et al. of potential search parameters to identify these diverged proteins will be useful to the those who work on the synaptonemal complex. This approach has the potential to applicable to other types of proteins that show rapid sequence divergence. As the mammalian, fly, and worm SC proteins all displayed different lengths and placements of their coiled-coil domains within their SC proteins this approach is limited by the availability of related identified sequences to the model organism of interest. Additionally, this approach may still yield multiple candidates that fit the structural parameters which will require additional means to ultimately identify the protein of interest. The data in the manuscript supports the authors' claims of structural conservation within SC proteins but only additional applications of their search methods will reveal how useful it is to search for other types of proteins based on structural features.

We thank the reviewer for their summary and feedback. We hope that with the ever-lowered costs of genome assembly and the expansion of CRISPR/Cas9 gene-editing capabilities, the pipeline we developed will be applicable to more clades and species. We agree that it will be interesting to expand our method beyond the SC. Going forward, we are excited to test whether it will enable us to identify other types of proteins, especially those that are part of condensates. In this light, our finding that centrosomal proteins are also enriched in the same evolutionary class as SC proteins is especially intriguing.

Reviewer #2 (Public Review):

In this article, Kursel and colleagues sought to identify evolutionary features of components of the SC the are evident in the absence of strict amino-acid conservation. After identifying three joint evolutionary properties of SC proteins - conservation of coiled-coil architecture, conservation of length and significant amino acid divergence - they show that these properties can be used to identify unknown SC proteins in divergent species. Overall, their general conclusion is very well supported and they do an excellent job functionally testing their approach by showing that one identified candidate for a novel SC protein in Pristionchus is in fact a component of the SC. In addition to providing new insight into the evolutionary forces that shape the evolution of SC proteins, this article provides new insight into how one might generally identify functionally similar or homologous proteins despite very deep divergence. Thus, this work has broader relevance to molecular evolution and evolution of protein structure.

There are some places where smaller conclusions need more support. In particular, it is not entirely clear that this triple pattern - conservation of coiled-coil architecture, conservation of length and significant amino acid divergence - is broadly applicable to SC components beyond Dipterans and Nematodes. In particular, the pattern is weaker in Eutherian mammals. Some further investigation is needed to claim that the pattern is similar in mammals. In addition, it is not clear if coiled-coil conservation rather than simply having a coiled-coil domain is important as a mark of SC proteins. A comparison of coiled-coil conservation among proteins that have coiled-coil domains would be needed for this conclusion. Finally, there should be some additional clarification that not all nematode SC proteins have a pattern of insertion and deletion that is limited to regions outside of the coil-coil domains.

We thank the reviewer for their appreciation of the broader impacts of our work to molecular evolution and for their suggestions for providing more support for our conclusions. We have addressed each of these points below (1. the evolutionary pattern in mammals, 2. the value of the coiled-coil conservation score, and 3. clarification of the indel analysis).

1) As suggested, we have added dot plots comparing mammalian SC proteins to all other mammalian proteins for the three metrics central to this manuscript - amino acid substitutions per site, coiled-coil conservation scores and coefficient of variation of protein length. The plots (shown here) can be found in Figure 3 – figure supplement 4.

These plots provide additional evidence that the evolutionary pattern of mammalian SC proteins is similar to (although weaker than) that of Caenorhabitis and Drosophila.

In panel (A), we show the median amino acid substitutions per site of SC proteins is higher than other proteins in mammals, although the difference is not significant. We discuss two reasons why the divergence trend is weaker for mammalian SC proteins in the results. Briefly summarized they are, 1. The overall divergence of the mammalian proteome is less than that of the Caenorhabditis or Drosophila proteome, and 2. Mammalian SC proteins may face additional evolutionary constraints due to novel functions including mammalian-specific protein interactions.

In panel (B), we show that mammalian SC proteins have a significantly higher coiled-coil conservation score than other proteins.

In panel (C), we show coefficient of variation of protein length for mammalian SC proteins is not significantly different than other proteins. We hypothesize that this could be due to gene annotation errors which plague even very high-quality genomes. For example, we found annotation errors in 23 (18%) of the 125 Caenorhabditis SC proteins examined in this study. Uncorrected, these errors often read as large insertions or deletions, and artificially large coefficient of variation. We use L. africana SYCE3 to demonstrate how potential annotation errors could impact our measure of length variation in mammalian SC proteins. L. africana SYCE3 has conspicuous N- and C-terminal extensions not found in any other SYCE3. Excluding that single protein - L. africana SYCE3 – reduces the average length variation from 29% to 4% in the SYCE3 orthogroup, below the median of other proteins. Correspondingly, the median SC coefficient of variation of protein length drops from 20% (unfilled black circle) to 12% (dashed, unfilled circle). While systematic manual annotation of the Eutherian mammals proteomes is beyond the scope of this manuscript, we added in the Discussion explicit reference to the implications of annotation errors on our ability to systematically address evolutionary pressures affecting indels.

2) We thank the reviewers for this important suggestion. Indeed, the inclusion of the few examples in Figure 2 were meant as demonstration rather than a statistical analysis. To create a group of proteins that would serve as appropriate control for conservation of the length and organization of the of coiled-coils, we selected orthogroups in which 90% of the proteins in the group had a coiled-coil domain of 21 amino acids or longer. This left 916 Caenorhabditis orthogroups including all SC proteins. We found that the median coiled-coil conservation score of SC proteins was significantly higher than that of the other coiled-coil proteins, confirming our comparisons to the entire proteome. We have included this analysis as a figure supplement to figure 2 (dot plot shown here and Figure 2 – figure supplement 1) and added text to the results and methods describing the analysis.

More broadly, this result suggests that our coiled-coil conservation score is more informative than a binary measure of coiled-coil domain prediction (i.e. presence/absence of coiled-coil). The additional information contained in the coiled-coil conservation score likely comes from the fact that we take into account whether or not the coiled-coil domains are aligned across species; which reflects a higher degree of secondary structure conservation. We believe that future work to develop better measures of conservation of secondary structures will hone our ability to identify conservation of other protein classes.

3) We have clarified this point in our revised manuscript, highlighting that when analyzed as a group, indels are excluded in coiled-coils of Caenorhabditis SC proteins, and that significance is also observed for specific SC proteins where enough indels are present to perform statistical tests. Two of the SC proteins, SYP-2 and SYP-3, had only two indels each, preventing us from performing tests of significance. We have also added text to the discussion directly addressing the limitations of automatically-assigned gene annotations on the ability to test evolutionary pressures on indels genome-wide.

Reviewer #3 (Public Review):

The manuscript "Unconventional conservation reveals structure-function relationships in the synaptonemal complex" by Kursel, Cope, and Rog, describes a novel bioinformatics analysis of proteins in the eukaryotic synaptonemal complex (SC). The SC is a highly conserved structure that links paired homologs in prophase of meiosis, and in most organisms is required for the successful completion of interhomolog recombination. An enigmatic feature of SC proteins is that they are highly diverged between organisms, to the point where they are nearly unrecognizable by sequence alone except among closely related organisms. Kursel et al show that within the Caenorhabditis family of nematodes, SC proteins show a reproducible pattern of coiled-coil segments and highly conserved overall length, while their primary sequences are extremely diverged. They use these findings to develop a method to identify new SC candidate proteins in a diverged nematode, Pristionchus pacificus, and confirm that one of these candidates is the main SC transverse filament protein in this organism. Finally, the authors expand their analysis to SC proteins in flies (Drosophila melanogaster and relatives) and eutherian mammals, and show similar findings in these protein families. In the discussion, the authors describe an interesting and compelling theory that the coiled coils of SC proteins directly support phase separation/condensation of these proteins to aid assembly of the SC superstructure.

Overall, this work is well done, the findings are well-supported, and are of interest to meiosis researchers; especially those working directly on the SC. The manuscript is also well put-together: I could barely find a typo. From a broader perspective, however, I'm not convinced that the work provides a new paradigm for thinking about "conservation" in protein families and how to best detect it. Methods that use structural information to detect homology between highly diverged proteins beyond the capabilities of BLAST or even PSI-BLAST are well-developed (e.g. PHYRE2, HHPred, and others). The use of coiled-coil length as a metric for conservation, while it works nicely in the case of SC proteins, is likely to not be generalizable to other protein families. Even within SC proteins, the method does not seem to scale past specific families to, say, allow identification of homology between distantly-related eukaryotic groups (e.g. between Caenorhabditis and Drosophila or Caenorhabditis and eutherian mammals). To be fair, this failure to scale is not because of any limitation with the method; rather, simply that SC proteins diverge quickly through evolution. Overall, however, these limitations seem to limit the application of this method to the specialized case of SC proteins, thus limiting the audience and scope of the work.

We appreciate the reviewer’s consideration of possible limitations of our study. However, we disagree that this method, and the insights gained from it, will be limited to SC proteins. A clear demonstration is that the centrosomal protein SPD-5 (Centrosomin in Drosophila, CdkRap2 in mammals) cannot be identified across clades using sequence homology despite performing a conserved and fundamental cellular function. We hypothesize that similar forces have shaped the evolution of SPD-5 and other centrosomal proteins that are enriched in the same evolutionary class as SC proteins (Figure 3 – figure supplement 1). Functional tests of these predictions will be an exciting area of future research.

As this review notes, an exciting hypothesis stemming from our work is that proteins with diverged primary sequence and conserved secondary structures (coiled-coils, disordered protein domains or others) will be over-represented in condensates. Anecdotally this is indeed true, as both the SC and the centrosome were shown to be condensates. The burgeoning interest in condensates, and the development of tools to study them in vivo and in vitro, are bound to test the broad applicability of this hypothesis.

Author Response:

Evaluation Summary:

The authors assessed multivariate relations between a dimensionality-reduced symptom space and brain imaging features, using a large database of individuals with psychosis-spectrum disorders (PSD). Demonstrating both high stability and reproducibility of their approaches, this work showed a promise that diagnosis or treatment of PSD can benefit from a proposed data-driven brain-symptom mapping framework. It is therefore of broad potential interest across cognitive and translational neuroscience.

We are very grateful for the positive feedback and the careful read of our paper. We would especially like to thank the Reviewers for taking the time to read this lengthy and complex manuscript and for providing their helpful and highly constructive feedback. Overall, we hope the Editor and the Reviewers will find that our responses address all the comments and that the requested changes and edits improved the paper.

Reviewer 1 (Public Review):

The paper assessed the relationship between a dimensionality-reduced symptom space and functional brain imaging features based on the large multicentric data of individuals with psychosis-spectrum disorders (PSD).

The strength of this study is that i) in every analysis, the authors provided high-level evidence of reproducibility in their findings, ii) the study included several control analyses to test other comparable alternatives or independent techniques (e.g., ICA, univariate vs. multivariate), and iii) correlating to independently acquired pharmacological neuroimaging and gene expression maps, the study highlighted neurobiological validity of their results.

Overall the study has originality and several important tips and guidance for behavior-brain mapping, although the paper contains heavy descriptions about data mining techniques such as several dimensionality reduction algorithms (e.g., PCA, ICA, and CCA) and prediction models.

We thank the Reviewer for their insightful comments and we appreciate the positive feedback. Regarding the descriptions of methods and analytical techniques, we have removed these descriptions out of the main Results text and figure captions. Detailed descriptions are still provided in the Methods, so that they do not detract from the core message of the paper but can still be referenced if a reader wishes to look up the details of these methods within the context of our analyses.

Although relatively minors, I also have few points on the weaknesses, including i) an incomplete description about how to tell the PSD effects from the normal spectrum, ii) a lack of overarching interpretation for other principal components rather than only the 3rd one, and iii) somewhat expected results in the stability of PC and relevant indices.

We are very appreciative of the constructive feedback and feel that these revisions have strengthened our paper. We have addressed these points in the revision as following:

i) We are grateful to the Reviewer for bringing up this point as it has allowed us to further explore the interesting observation we made regarding shared versus distinct neural variance in our data. It is important to not confuse the neural PCA (i.e. the independent neural features that can be detected in the PSD and healthy control samples) versus the neuro-behavioral mapping. In other words, both PSD patients and healthy controls are human and therefore there are a number of neural functions that both cohorts exhibit that may have nothing to do with the symptom mapping in PSD patients. For instance, basic regulatory functions such as control of cardiac and respiratory cycles, motor functions, vision, etc. We hypothesized therefore that there are more common than distinct neural features that are on average shared across humans irrespective of their psychopathology status. Consequently, there may only be a ‘residual’ symptom-relevant neural variance. Therefore, in the manuscript we bring up the possibility that a substantial proportion of neural variance may not be clinically relevant. If this is in fact true then removing the shared neural variance between PSD and CON should not drastically affect the reported symptom-neural univariate mapping solution, because this common variance does not map to clinical features and therefore is orthogonal statistically. We have now verified this hypothesis quantitatively and have added extensive analyses to highlight this important observation made the the Reviewer. We first conducted a PCA using the parcellated GBC data from all 436 PSD and 202 CON (a matrix with dimensions 638 subjects x 718 parcels). We will refer to this as the GBC-PCA to avoid confusion with the symptom/behavioral PCA described elsewhere in the manuscript. This GBC-PCA resulted in 637 independent GBC-PCs. Since PCs are orthogonal to each other, we then partialled out the variance attributable to GBC-PC1 from the PSD data by reconstructing the PSD GBC matrix using only scores and coefficients from the remaining 636 GBC-PCs (GBˆCwoP C1). We then reran the univariate regression as described in Fig. 3, using the same five symptom PC scores across 436 PSD. The results are shown in Fig. S21 and reproduced below. Removing the first PC of shared neural variance (which accounted for about 15.8% of the total GBC variance across CON and PSD) from PSD data attenuated the statistics slightly (not unexpected as the variance was by definition reduced) but otherwise did not strongly affect the univariate mapping solution.

We repeated the symptom-neural regression next with the first 2 GBC-PCs partialled out of the PSD data Fig. S22, with the first 3 PCs parsed out Fig. S23, and with the first 4 neural PCs parsed out Fig. S24. The symptom-neural maps remain fairly robust, although the similarity with the original βP CGBC maps does drop as more common neural variance is parsed out. These figures are also shown below:

Fig. S21. Comparison between the PSD βP CGBC maps computed using GBC and GBC with the first neural PC parsed out. If a substantial proportion of neural variance is not be clinically relevant, then removing the shared neural variance between PSD and CON should not drastically affect the reported symptom-neural univariate mapping solution, because this common variance will not map to clinical features. We therefore performed a PCA on CON and PSD GBC to compute the shared neural variance (see Methods), and then parsed out the first GBC-PC from the PSD GBC data (GBˆCwoP C1). We then reran the univariate regression as described in Fig. 3, using the same five symptom PC scores across 436 PSD. (A) The βP C1GBC map, also shown in Fig. S10. (B) The first GBC-PC accounted for about 15.8% of the total GBC variance across CON and PSD. Removing GBC-PC1 from PSD data attenuated the βP C1GBC statistics slightly (not unexpected as the variance was by definition reduced) but otherwise did not strongly affect the univariate mapping solution. (C) Correlation across 718 parcels between the two βP C1GBC map shown in A and B. (D-O) The same results are shown for βP C2GBC to βP C5GBC maps.

Fig. S22. Comparison between the PSD βP CGBC maps computed using GBC and GBC with the first two neural PCs parsed out. We performed a PCA on CON and PSD GBC and then parsed out the first three GBC-PC from the PSD GBC data (GBˆCwoP C1−2, see Methods). We then reran the univariate regression as described in Fig. 3, using the same five symptom PC scores across 436 PSD. (A) The βP C1GBC map, also shown in Fig. S10. (B) The second GBC-PC accounted for about 9.5% of the total GBC variance across CON and PSD. (C) Correlation across 718 parcels between the two βP C1GBC map shown in A and B. (D-O) The same results are shown for βP C2GBC to βP C5GBC maps.

Fig. S23. Comparison between the PSD βP CGBC maps computed using GBC and GBC with the first three neural PCs parsed out. We performed a PCA on CON and PSD GBC and then parsed out the first three GBC-PC from the PSD GBC data (GBˆCwoP C1−3, see Methods). We then reran the univariate regression as described in Fig. 3, using the same five symptom PC scores across 436 PSD. (A) The βP C1GBC map, also shown in Fig. S10. (B) The second GBC-PC accounted for about 9.5% of the total GBC variance across CON and PSD. (C) Correlation across 718 parcels between the two βP C1GBC map shown in A and B. (D-O) The same results are shown for βP C2GBC to βP C5GBC maps.

Fig. S24. Comparison between the PSD βP CGBC maps computed using GBC and GBC with the first four neural PCs parsed out. We performed a PCA on CON and PSD GBC and then parsed out the first four GBC-PC from the PSD GBC data (GBˆCwoP C1−4, see Methods). We then reran the univariate regression as described in Fig. 3, using the same five symptom PC scores across 436 PSD. (A) The βP C1GBC map, also shown in Fig. S10. (B) The second GBC-PC accounted for about 9.5% of the total GBC variance across CON and PSD. (C) Correlation across 718 parcels between the two βP C1GBC map shown in A and B. (D-O) The same results are shown for βP C2GBC to βP C5GBC maps.

For comparison, we also computed the βP CGBC maps for control subjects, shown in Fig. S11. In support of the βP CGBC in PSD being circuit-relevant, we observed only mild associations between GBC and PC scores in healthy controls:

Results: All 5 PCs captured unique patterns of GBC variation across the PSD (Fig. S10), which were not observed in CON (Fig. S11). ... Discussion: On the contrary, this bi-directional “Psychosis Configuration” axis also showed strong negative variation along neural regions that map onto the sensory-motor and associative control regions, also strongly implicated in PSD (1, 2). The “bi-directionality” property of the PC symptom-neural maps may thus be desirable for identifying neural features that support individual patient selection. For instance, it may be possible that PC3 reflects residual untreated psychosis symptoms in this chronic PSD sample, which may reveal key treatment neural targets. In support of this circuit being symptom-relevant, it is notable that we observed a mild association between GBC and PC scores in the CON sample (Fig. S11).

ii) In our original submission we spotlighted PC3 because of its pattern of loadings on to hallmark symptoms of PSD, including strong positive loadings across Positive symptom items in the PANSS and conversely strong negative loadings on to most Negative items. It was necessary to fully examine this dimension in particular because these are key characteristics of the target psychiatric population, and we found that the focus on PC3 was innovative because it provided an opportunity to quantify a fully data-driven dimension of symptom variation that is highly characteristic of the PSD patient population. Additionally, this bi-directional axis captured shared variance from measures in other traditional symptoms factors, such the PANSS General factor and cognition. This is a powerful demonstration of how data-driven techniques such as PCA can reveal properties intrinsic to the structure of PSD-relevant symptom data which may in turn improve the mapping of symptom-neural relationships. We refrained from explaining each of the five PCs in detail in the main text as we felt that it would further complicate an already dense manuscript. Instead, we opted to provide the interpretation and data from all analyses for all five PCs in the Supplement. However, in response to the Reviewers’ thoughtful feedback that more focus should be placed on other components, we have expanded the presentation and discussion of all five components (both regarding the symptom profiles and neural maps) in the main text:

Results: Because PC3 loads most strongly on to hallmark symptoms of PSD (including strong positive loadings across PANSS Positive symptom measures in the PANSS and strong negative loadings onto most Negative measures), we focus on this PC as an opportunity to quantify an innovative, fully data-driven dimension of symptom variation that is highly characteristic of the PSD patient population. Additionally, this bi-directional symptom axis captured shared variance from measures in other traditional symptoms factors, such the PANSS General factor and cognition. We found that the PC3 result provided a powerful empirical demonstration of how using a data-driven dimensionality-reduced solution (via PCA) can reveal novel patterns intrinsic to the structure of PSD psychopathology.

iii) We felt that demonstrating the stability of the PCA solution was extremely important, given that this degree of rigor has not previously been tested using broad behavioral measures across psychosis symptoms and cognition in a cross-diagnostic PSD sample. Additionally, we demonstrated reproducibility of the PCA solution using independent split-half samples. Furthermore, we derived stable neural maps using the PCA solution. In our original submission we show that the CCA solution was not reproducible in our dataset. Following the Reviewers’ feedback, we computed the estimated sample sizes needed to sufficiently power our multivariate analyses for stable/reproducible solutions. using the methods in (3). These results are discussed in detail in our resubmitted manuscript and in our response to the Critiques section below.

Reviewer 2 (Public Review):

The work by Ji et al is an interesting and rather comprehensive analysis of the trend of developing data-driven methods for developing brain-symptom dimension biomarkers that bring a biological basis to the symptoms (across PANSS and cognitive features) that relate to psychotic disorders. To this end, the authors performed several interesting multivariate analyses to decompose the symptom/behavioural dimensions and functional connectivity data. To this end, the authors use data from individuals from a transdiagnostic group of individuals recruited by the BSNIP cohort and combine high-level methods in order to integrate both types of modalities. Conceptually there are several strengths to this paper that should be applauded. However, I do think that there are important aspects of this paper that need revision to improve readability and to better compare the methods to what is in the field and provide a balanced view relative to previous work with the same basic concepts that they are building their work around. Overall, I feel as though the work could advance our knowledge in the development of biomarkers or subject level identifiers for psychiatric disorders and potentially be elevated to the level of an individual "subject screener". While this is a noble goal, this will require more data and information in the future as a means to do this. This is certainly an important step forward in this regard.

We thank the Reviewer for their insightful and constructive comments about our manuscript. We have revised the text to make it easier to read and to clarify our results in the context of prior works in the field. We fully agree that a great deal more work needs to be completed before achieving single-subject level treatment selection, but we hope that our manuscript provides a helpful step towards this goal.

Strengths:

• Combined analysis of canonical psychosis symptoms and cognitive deficits across multiple traditional psychosis-related diagnoses offers one of the most comprehensive mappings of impairments experienced within PSD to brain features to date
• Cross-validation analyses and use of various datasets (diagnostic replication, pharmacological neuroimaging) is extremely impressive, well motivated, and thorough. In addition the authors use a large dataset and provide "out of sample" validity
• Medication status and dosage also accounted for
• Similarly, the extensive examination of both univariate and multivariate neuro-behavioural solutions from a methodological viewpoint, including the testing of multiple configurations of CCA (i.e. with different parcellation granularities), offers very strong support for the selected symptom-to-neural mapping
• The plots of the obtained PC axes compared to those of standard clinical symptom aggregate scales provide a really elegant illustration of the differences and demonstrate clearly the value of data-driven symptom reduction over conventional categories
• The comparison of the obtained neuro-behavioural map for the "Psychosis configuration" symptom dimension to both pharmacological neuroimaging and neural gene expression maps highlights direct possible links with both underlying disorder mechanisms and possible avenues for treatment development and application
• The authors' explicit investigation of whether PSD and healthy controls share a major portion of neural variance (possibly present across all people) has strong implications for future brain-behaviour mapping studies, and provides a starting point for narrowing the neural feature space to just the subset of features showing symptom-relevant variance in PSD

We are very grateful for the positive feedback. We would like to thank the Reviewers for taking the time to read this admittedly dense manuscript and for providing their helpful critique.

Critiques:

• Overall I found the paper very hard to read. There are abbreviation everywhere for every concept that is introduced. The paper is methods heavy (which I am not opposed to and quite like). It is clear that the authors took a lot of care in thinking about the methods that were chosen. That said, I think that the organization would benefit from a more traditional Intro, Methods, Results, and Discussion formatting so that it would be easier to parse the Results. The figures are extremely dense and there are often terms that are coined or used that are not or poorly defined.

We appreciate the constructive feedback around how to remove the dense content and to pay more attention to the frequency of abbreviations, which impact readability. We implemented the strategies suggested by the Reviewer and have moved the Methods section after the Introduction to make the subsequent Results section easier to understand and contextualize. For clarity and length, we have moved methodological details previously in the Results and figure captions to the Methods (e.g. descriptions of dimensionality reduction and prediction techniques). This way, the Methods are now expanded for clarity without detracting from the readability of the core results of the paper. Also, we have also simplified the text in places where there was room for more clarity. For convenience and ease of use of the numerous abbreviations, we have also added a table to the Supplement (Supplementary Table S1).

• One thing I found conceptually difficult is the explicit comparison to the work in the Xia paper from the Satterthwaite group. Is this a fair comparison? The sample is extremely different as it is non clinical and comes from the general population. Can it be suggested that the groups that are clinically defined here are comparable? Is this an appropriate comparison and standard to make. To suggest that the work in that paper is not reproducible is flawed in this light.

This is an extremely important point to clarify and we apologize that we did not make it sufficiently clear in the initial submission. Here we are not attempting to replicate the results of Xia et al., which we understand were derived in a fundamentally different sample than ours both demographically and clinically, with testing very different questions. Rather, this paper is just one example out of a number of recent papers which employed multivariate methods (CCA) to tackle the mapping between neural and behavioral features. The key point here is that this approach does not produce reproducible results due to over-fitting, as demonstrated robustly in the present paper. It is very important to highlight that in fact we did not single out any one paper when making this point. In fact, we do not mention the Xia paper explicitly anywhere and we were very careful to cite multiple papers in support of the multivariate over-fitting argument, which is now a well-know issue (4). Nevertheless, the Reviewers make an excellent point here and we acknowledge that while CCA was not reproducible in the present dataset, this does not explicitly imply that the results in the Xia et al. paper (or any other paper for that matter) are not reproducible by definition (i.e. until someone formally attempts to falsify them). We have made this point explicit in the revised paper, as shown below. Furthermore, in line with the provided feedback, we also applied the multivariate power calculator derived by Helmer et al. (3), which quantitatively illustrates the statistical point around CCA instability.

Results: Several recent studies have reported “latent” neuro-behavioral relationships using multivariate statistics (5–7), which would be preferable because they simultaneously solve for maximal covariation across neural and behavioral features. Though concerns have emerged whether such multivariate results will replicate due to the size of the feature space relative to the size of the clinical samples (4), Given the possibility of deriving a stable multivariate effect, here we tested if results improve with canonical correlation analysis (CCA) (8) which maximizes relationships between linear combinations of symptom (B) and neural features (N) across all PSD (Fig. 5A).

Discussion: Here we attempted to use multivariate solutions (i.e. CCA) to quantify symptom and neural feature co- variation. In principle, CCA is well-suited to address the brain-behavioral mapping problem. However, symptom-neural mapping using CCA across either parcel-level or network-level solutionsin our sample was not reproducible even when using a low-dimensional symptom solution and parcellated neural data as a starting point. Therefore, while CCA (and related multivariate methods such as partial least squares) are theoretically appropriate and may be helped by regularization methods such as sparse CCA, in practice many available psychiatric neuroimaging datasets may not provide sufficient power to resolve stable multivariate symptom-neural solutions (3). A key pressing need for forthcoming studies will be to use multivariate power calculators to inform sample sizes needed for resolving stable symptom-neural geometries at the single subject level. Of note, though we were unable to derive a stable CCA in the present sample, this does not imply that the multivariate neuro-behavioral effect may not be reproducible with larger effect sizes and/or sample sizes. Critically, this does highlight the importance of power calculations prior to computing multivariate brain-behavioral solutions (3).

• Why was PCA selected for the analysis rather than ICA? Authors mention that PCA enables the discovery of orthogonal symptom dimensions, but don't elaborate on why this is expected to better capture behavioural variation within PSD compared to non-orthogonal dimensions. Given that symptom and/or cognitive items in conventional assessments are likely to be correlated in one way or another, allowing correlations to be present in the low-rank behavioural solution may better represent the original clinical profiles and drive more accurate brain-behaviour mapping. Moreover, as alluded to in the Discussion, employing an oblique rotation in the identification of dimensionality-reduced symptom axes may have actually resulted in a brain-behaviour space that is more generalizable to other psychiatric spectra. Why not use something more relevant to symptom/behaviour data like a factor analysis?

This is a very important point! We agree with the Reviewer that an oblique solution may better fit the data. For this reason, we performed an ICA as shown in the Supplement. We chose to show PCA for the main analyses here because it is a deterministic solution and the number of significant components could be computed via permutation testing. Importantly, certain components from the ICA solution in this sample were highly similar to the PCs shown in the main solution (Supplementary Note 1), as measured by comparing the subject behavioral scores (Fig. S4), and neural maps (Fig. S13). However, notably, certain components in the ICA and PCA solutions did not appear to have a one-to-one mapping (e.g. PCs 1-3 and ICs 1-3). The orthogonality of the PCA solution forces the resulting components to capture maximally separated, unique symptom variance, which in turn map robustly on to unique neural circuits. We observed that the data may be distributed in such a way that in the ICA highly correlated independent components emerge, which do not maximally separate the symptom variance associate with neural variance. We demonstrate this by plotting the relationship between parcel beta coefficients for the βP C3GBC map versus the βIC2GBC and βIC3GBC maps. The sigmoidal shape of the distribution indicates an improvement in the Z-statistics for the βP C3GBC map relative to the βIC2GBC and βIC3GBC maps. We have added this language to the main text Results:

Notably, independent component analysis (ICA), an alternative dimensionality reduction procedure which does not enforce component orthogonality, produced similar effects for this PSD sample, see Supplementary Note 1 & Fig. S4A). Certain pairs of components between the PCA and ICA solutions appear to be highly similar and exclusively mapped (IC5 and PC4; IC4 and PC5) (Fig. S4B). On the other hand, PCs 1-3 and ICs 1-3 do not exhibit a one-to-one mapping. For example, PC3 appears to correlate positively with IC2 and equally strongly negatively with IC3, suggesting that these two ICs are oblique to the PC and perhaps reflect symptom variation that is explained by a single PC. The orthogonality of the PCA solution forces the resulting components to capture maximally separated, unique symptom variance, which in turn map robustly on to unique neural circuits. We observed that the data may be distributed in such a way that in the ICA highly correlated independent components emerge, which do not maximally separate the symptom variance associate with neural variance. We demonstrate this by plotting the relationship between parcel beta coefficients for the βP C3GBC map versus the βIC2GBC and βIC3GBC maps Fig. ??G). The sigmoidal shape of the distribution indicates an improvement in the Z-statistics for the βP C3GBC map relative to the βIC2GBC and βIC3GBC maps.

Additionally, the Reviewer raises an important point, and we agree that orthogonal versus oblique solutions warrant further investigation especially with regards to other psychiatric spectra and/or other stages in disease progression. For example, oblique components may better capture dimensions of behavioral variation in prodromal individuals, as these individuals are in the early stages of exhibiting psychosis-relevant symptoms and may show early diverging of dimensions of behavioral variation. We elaborate on this further in the Discussion:

Another important aspect that will require further characterization is the possibility of oblique axes in the symptom-neural geometry. While orthogonal axes derived via PCA were appropriate here and similar to the ICA-derived axes in this solution, it is possible that oblique dimensions more clearly reflect the geometry of other psychiatric spectra and/or other stages in disease progression. For example, oblique components may better capture dimensions of neuro-behavioral variation in a sample of prodromal individuals, as these patients are exhibiting early-stage psychosis-like symptoms and may show signs of diverging along different trajectories.

Critically, these factors should constitute key extensions of an iteratively more robust model for indi- vidualized symptom-neural mapping across the PSD and other psychiatric spectra. Relatedly, it will be important to identify the ‘limits’ of a given BBS solution – namely a PSD-derived effect may not generalize into the mood spectrum (i.e. both the symptom space and the resulting symptom-neural mapping is orthogonal). It will be important to evaluate if this framework can be used to initialize symptom-neural mapping across other mental health symptom spectra, such as mood/anxiety disorders.

• The gene expression mapping section lacks some justification for why the 7 genes of interest were specifically chosen from among the numerous serotonin and GABA receptors and interneuron markers (relevant for PSD) available in the AHBA. Brief reference to the believed significance of the chosen genes in psychosis pathology would have helped to contextualize the observed relationship with the neuro-behavioural map.

We thank the Reviewer for providing this suggestion and agree that it will strengthen the section on gene expression analysis. Of note, we did justify the choice for these genes, but we appreciate the opportunity to expand on the neurobiology of selected genes and their relevance to PSD. We have made these edits to the text:

We focus here on serotonin receptor subunits (HTR1E, HTR2C, HTR2A), GABA receptor subunits (GABRA1, GABRA5), and the interneuron markers somatostatin (SST) and parvalbumin (PVALB). Serotonin agonists such as LSD have been shown to induce PSD-like symptoms in healthy adults (9) and the serotonin antagonism of “second-generation” antipsychotics are thought to contribute to their efficacy in targeting broad PSD symptoms (10–12). Abnormalities in GABAergic interneurons, which provide inhibitory control in neural circuits, may contribute to cognitive deficits in PSD (13–15) and additionally lead to downstream excitatory dysfunction that underlies other PSD symptoms (16, 17). In particular, a loss of prefrontal parvalbumin-expression fast-spiking interneurons has been implicated in PSD (18–21).

• What the identified univariate neuro-behavioural mapping for PC3 ("psychosis configuration") actually means from an empirical or brain network perspective is not really ever discussed in detail. E.g., in Results, "a high positive PC3 score was associated with both reduced GBC across insular and superior dorsal cingulate cortices, thalamus, and anterior cerebellum and elevated GBC across precuneus, medial prefrontal, inferior parietal, superior temporal cortices and posterior lateral cerebellum." While the meaning and calculation of GBC can be gleaned from the Methods, a direct interpretation of the neuro-behavioural results in terms of the types of symptoms contributing to PC3 and relative hyper-/hypo-connectivity of the DMN compared to e.g. healthy controls could facilitate easier comparisons with the findings of past studies (since GBC does not seem to be a very commonly-used measure in the psychosis fMRI literature). Also important since GBC is a summary measure of the average connectivity of a region, and doesn't provide any specificity in terms of which regions in particular are more or less connected within a functional network (an inherent limitation of this measure which warrants further attention).

We acknowledge that GBC is a linear combination measure that by definition does not provide information on connectivity between any one specific pair of neural regions. However, as shown by highly robust and reproducible neurobehavioral maps, GBC seems to be suitable as a first-pass metric in the absence of a priori assumptions of how specific regional connectivity may map to the PC symptom dimensions, and it has been shown to be sensitive to altered patterns of overall neural connectivity in PSD cohorts (22–25) as well as in models of psychosis (9, 26). Moreover, it is an assumption free method for dimensionality reduction of the neural connectivity matrix (which is a massive feature space). Furthermore, GBC provides neural maps (where each region can be represented by a value, in contrast to full functional connectivity matrices), which were necessary for quantifying the relationship with independent molecular benchmark maps (i.e. pharmacological maps and gene expression maps). We do acknowledge that there are limitations to the method which we now discuss in the paper. Furthermore we agree with the Reviewer that the specific regions implicated in these symptom-neural relationships warrants a more detailed investigation and we plan to develop this further in future studies, such as with seed-based functional connectivity using regions implicated in PSD (e.g. thalamus (2, 27)) or restricted GBC (22) which can summarize connectivity information for a specific network or subset of neural regions. We have provided elaboration and clarification regarding this point in the Discussion:

Another improvement would be to optimize neural data reduction sensitivity for specific symptom variation (28). We chose to use GBC for our initial geometry characterizations as it is a principled and assumption-free data-reduction metric that captures (dys)connectivity across the whole brain and generates neural maps (where each region can be represented by a value, in contrast to full functional connectivity matrices) that are necessary for benchmarking against molecular imaging maps. However, GBC is a summary measure that by definition does not provide information regarding connectivity between specific pairs of neural regions, which may prove to be highly symptom-relevant and informative. Thus symptom-neural relationships should be further explored with higher-resolution metrics, such as restricted GBC (22) which can summarize connectivity information for a specific network or subset of neural regions, or seed-based FC using regions implicated in PSD (e.g. thalamus (2, 27)).

• Possibly a nitpick, but while the inclusion of cognitive measures for PSD individuals is a main (self-)selling point of the paper, there's very limited focus on the "Cognitive functioning" component (PC2) of the PCA solution. Examining Fig. S8K, the GBC map for this cognitive component seems almost to be the inverse for that of the "Psychosis configuration" component (PC3) focused on in the rest of the paper. Since PC3 does not seem to have high loadings from any of the cognitive items, but it is known that psychosis spectrum individuals tend to exhibit cognitive deficits which also have strong predictive power for illness trajectory, some discussion of how multiple univariate neuro-behavioural features could feasibly be used in conjunction with one another could have been really interesting.

This is an important piece of feedback concerning the cognitive measure aspect of the study. As the Reviewer recognizes, cognition is a core element of PSD symptoms and the key reason for including this symptom into the model. Notably, the finding that one dimension captures a substantial proportion of cognitive performance-related variance, independent of other residual symptom axes, has not previously been reported and we fully agree that expanding on this effect is important and warrants further discussion. We would like to take two of the key points from the Reviewers’ feedback and expand further. First, we recognize that upon qualitative inspection PC2 and PC3 neural maps appear strongly anti-correlated. However, as demonstrated in Fig. S9O, PC2 and PC3 maps were anti-correlated at r=-0.47. For comparison, the PC2 map was highly anti-correlated with the BACS composite cognitive map (r=-0.81). This implies that the PC2 map in fact reflects unique neural circuit variance that is relevant for cognition, but not necessarily an inverse of the PC3.

In other words, these data suggest that there are PSD patients with more (or less) severe cognitive deficits independent of any other symptom axis, which would be in line with the observation that these symptoms are not treatable with antipsychotic medication (and therefore should not correlate with symptoms that are treatable by such medications; i.e. PC3). We have now added these points into the revised paper:

Results Fig. 1E highlights loading configurations of symptom measures forming each PC. To aid interpretation, we assigned a name for each PC based on its most strongly weighted symptom measures. This naming is qualitative but informed by the pattern of loadings of the original 36 symptom measures (Fig. 1). For example, PC1 was highly consistent with a general impairment dimension (i.e. “Global Functioning”); PC2 reflected more exclusively variation in cognition (i.e. “Cognitive Functioning”); PC3 indexed a complex configuration of psychosis-spectrum relevant items (i.e. “Psy- chosis Configuration”); PC4 generally captured variation mood and anxiety related items (i.e. “Affective Valence”); finally, PC5 reflected variation in arousal and level of excitement (i.e. “Agitation/Excitation”). For instance, a generally impaired patient would have a highly negative PC1 score, which would reflect low performance on cognition and elevated scores on most other symptomatic items. Conversely, an individual with a high positive PC3 score would exhibit delusional, grandiose, and/or hallucinatory behavior, whereas a person with a negative PC3 score would exhibit motor retardation, social avoid- ance, possibly a withdrawn affective state with blunted affect (29). Comprehensive loadings for all 5 PCs are shown in Fig. 3G. Fig. 1F highlights the mean of each of the 3 diagnostic groups (colored spheres) and healthy controls (black sphere) projected into a 3-dimensional orthogonal coordinate system for PCs 1,2 & 3 (x,y,z axes respectively; alternative views of the 3-dimensional coordinate system with all patients projected are shown in Fig. 3). Critically, PC axes were not parallel with traditional aggregate symptom scales. For instance, PC3 is angled at 45◦ to the dominant direction of PANSS Positive and Negative symptom variation (purple and blue arrows respectively in Fig. 1F). ... Because PC3 loads most strongly on to hallmark symptoms of PSD (including strong positive load- ings across PANSS Positive symptom measures in the PANSS and strong negative loadings onto most Negative measures), we focus on this PC as an opportunity to quantify an innovative, fully data-driven dimension of symptom variation that is highly characteristic of the PSD patient population. Additionally, this bi-directional symptom axis captured shared variance from measures in other traditional symptoms factors, such the PANSS General factor and cognition. We found that the PC3 result provided a powerful empirical demonstration of how using a data-driven dimensionality-reduced solution (via PCA) can reveal novel patterns intrinsic to the structure of PSD psychopathology.

Another nitpick, but the Y axes of Fig. 8C-E are not consistent, which causes some of the lines of best fit to be a bit misleading (e.g. GABRA1 appears to have a more strongly positive gene-PC relationship than HTR1E, when in reality the opposite is true.)

We have scaled each axis to best show the data in each plot but see how this is confusing and recognise the need to correct this. We have remade the plots with consistent axes labelling.

• The authors explain the apparent low reproducibility of their multivariate PSD neuro-behavioural solution using the argument that many psychiatric neuroimaging datasets are too small for multivariate analyses to be sufficiently powered. Applying an existing multivariate power analysis to their own data as empirical support for this idea would have made it even more compelling. The following paper suggests guidelines for sample sizes required for CCA/PLS as well as a multivariate calculator: Helmer, M., Warrington, S. D., Mohammadi-Nejad, A.-R., Ji, J. L., Howell, A., Rosand, B., Anticevic, A., Sotiropoulos, S. N., & Murray, J. D. (2020). On stability of Canonical Correlation Analysis and Partial Least Squares with application to brain-behavior associations (p. 2020.08.25.265546). https://doi.org/10.1101/2020.08.25.265546

We deeply appreciate the Reviewer’s suggestion and the opportunity to incorporate the methods from the Helmer et al. paper. We now highlight the importance of having sufficiently powered samples for multivariate analyses in our other manuscript first-authored by our colleague Dr. Markus Helmer (3). Using the method described in the above paper (GEMMR version 0.1.2), we computed the estimated sample sizes required to power multivariate CCA analyses with 718 neural features and 5 behavioral (PC) features (i.e. the feature set used throughout the rest of the paper):

As argued in Helmer et al., rtrue is likely below 0.3 in many cases, thus the estimated sample size of 33k is likely a lower bound for the required sample size for sufficiently-powered CCA analyses using the 718+5 features leveraged throughout the univariate analyses in the present manuscript. This number is two orders of magnitude greater than our available sample (and at least one order of magnitude greater than any single existing clinical dataset). Even if rtrue is 0.5, a sample size of ∼10k would likely be required.

As argued in Helmer et al., rtrue is likely below 0.3 in many cases, thus the estimated sample size of 33k is likely a lower bound for the required sample size for sufficiently-powered CCA analyses using the 718+5 features leveraged throughout the univariate analyses in the present manuscript. This number is two orders of magnitude greater than our available sample (and at least one order of magnitude greater than any single existing clinical dataset). Even if rtrue is 0.5, a sample size of ∼10k would likely be required. We also computed the estimated sample sizes required for 180 neural features (symmetrized neural cortical parcels) and 5 symptom PC features, consistent with the CCA reported in our main text:

Assuming that rtrue is likely below 0.3, this minimal required sample size remains at least an order of magnitude greater than the size of our present sample, consistent with the finding that the CCA solution computed using these data was unstable. As a lower limit for the required sample size plausible using the feature sets reported in our paper, we additionally computed for comparison the estimated N needed with the smallest number of features explored in our analyses, i.e. 12 neural functional network features and 5 symptom PC features:

These required sample sizes are closer to the N=436 used in the present sample and samples reported in the clinical neuroimaging literature. This is consistent with the observation that when using 12 neural and 5 symptom features (Fig. S15C) the detected canonical correlation r = 0.38 for CV1 is much lower (and likely not inflated due to overfitting) and may be closer to the true effect because with the n=436 this effect is resolvable. This is in contrast to the 180 neural features and 5 symptom feature CCA solution where we observed a null CCA effect around r > 0.6 across all 5 CVs. This clearly highlights the inflation of the effect in the situation where the feature space grows. There is no a priori plausible reason to believe that the effect for 180 vs. 5 feature mapping is literally double the effect when using 12 vs. 5 feature mapping - especially as the 12 features are networks derived from the 180 parcels (i.e. the effect should be comparable rather than 2x smaller). Consequently, if the true CCA effect with 180 vs. 5 features was actually in the more comparable r = 0.38, we would need >5,000 subjects to resolve a reproducible neuro-behavioral CCA map (an order of magnitude more than in the BSNIP sample). Moreover, to confidently detect effects if rtrue is actually less than 0.3, we would require a sample size >8,145 subjects. We have added this to the Results section on our CCA results:

Next, we tested if the 180-parcel CCA solution is stable and reproducible, as done with PC-to-GBC univariate results. The CCA solution was robust when tested with k-fold and leave-site-out cross- validation (Fig. S16) likely because these methods use CCA loadings derived from the full sample. However, the CCA loadings did not replicate in non-overlapping split-half samples (Fig. 5L, see see Supplementary Note 4). Moreover, a leave-one-subject-out cross-validation revealed that removing a single subject from the sample affected the CCA solution such that it did not generalize to the left-out subject (Fig. 5M). This is in contrast to the PCA-to-GBC univariate mapping, which was substantially more reproducible for all attempted cross-validations relative to the CCA approach. This is likely because substantially more power is needed to resolve a stable multivariate neuro-behavioral effect with this many features. Indeed, a multivariate power analysis using 180 neural features and 5 symptom features, and assuming a true canonical correlation of r = 0.3, suggests that a minimal sample size of N = 8145 is needed to sufficiently detect the effect (3), an order of magnitude greater than the available sample size. Therefore, we leverage the univariate neuro-behavioral result for subsequent subject-specific model optimization and comparisons to molecular neuroimaging maps.

Additionally, we added the following to Supplementary Note 4: Establishing the Reproducibility of the CCA Solution:

Here we outline the details of the split-half replication for the CCA solution. Specifically, the full patient sample was randomly split (referred to as “H1” and “H2” respectively), while preserving the proportion of patients in each diagnostic group. Then, CCA was performed independently for H1 and H2. While the loadings for behavioral PCs and original behavioral items are somewhat similar (mean r 0.5) between the two CCAs in each run, the neural loadings were not stable across H1 and H2 CCA solutions. Critically, CCA results did not perform well for leave-one-subject-out cross-validation (Fig. 5M). Here, one patient was held out while CCA was performed using all data from the remaining 435 patients. The loadings matrices Ψ and Θ from the CCA were then used to calculate the “predicted” neural and behavioral latent scores for all 5 CVs for the patient that was held out of the CCA solution. This process was repeated for every patient and the final result was evaluated for reproducibility. As described in the main text, this did not yield reproducible CCA effects (Fig. 5M). Of note, CCA may yield higher reproducibility if the neural feature space were to be further reduced. As noted, our approach was to first parcellate the BOLD signal and then use GBC as a data-driven method to yield a neuro-biologically and quantitatively interpretable neural data reduction, and we additionally symmetrized the result across hemispheres. Nevertheless, in sharp contrast to the PCA univariate feature selection approach, the CCA solutions were still not stable in the present sample size of N = 436. Indeed, a multivariate power analysis (3) estimates that the following sample sizes will be required to sufficiently power a CCA between 180 neural features and 5 symptom features, at different levels of true canonical correlation (rtrue):

To test if further neural feature space reduction may be improve reproducibility, we also evaluated CCA solutions with neural GBC parcellated according to 12 brain-wide functional networks derived from the recent HCP driven network parcellation (30). Again, we computed the CCA for all 36 item-level symptom as well as 5 PCs (Fig. S15). As with the parcel-level effects, the network-level CCA analysis produced significant results (for CV1 when using 36 item-level scores and for all 5 CVs when using the 5 PC-derived scores). Here the result produced much lower canonical correlations ( 0.3-0.5); however, these effects (for CV1) clearly exceeded the 95% confidence interval generated via random permutations, suggesting that they may reflect the true canonical correlation. We observed a similar result when we evaluated CCAs computed with neural GBC from 192 symmetrized subcortical parcels and 36 symptoms or 5 PCs (Fig. S14). In other words, data-reducing the neural signal to 12 functional networks likely averaged out parcel-level information that may carry symptom-relevant variance, but may be closer to capturing the true effect. Indeed, the power analysis suggests that the current sample size is closer to that needed to detect an effect with 12 + 5 features:

Note that we do not present a CCA conducted with parcels across the whole brain, as the number of variables would exceed the number of observations. However, the multivariate power analysis using 718 neural features and 5 symptom features estimates that the following sample sizes would be required to detect the following effects:

This analysis suggests that even the lowest bound of 10k samples exceeds the present available sample size by two orders of magnitude.

We have also added Fig. S19, illustrating these power analyses results:

Fig. S19. Multivariate power analysis for CCA. Sample sizes were calculated according to (3), see also https://gemmr.readthedocs.io/en/latest/. We computed the multivariate power analyses for three versions of CCA reported in this manuscript: i) 718 neural vs. 5 symptom features; ii) 180 neural vs. 5 symptom features; iii) 12 neural vs. 5 symptom features. (A) At different levels of features, the ratio of samples (i.e. subjects) required per feature to derive a stable CCA solution remains approximately the same across all values of rtrue. As discussed in (3), at rtrue = 0.3 the number of samples required per feature is about 40, which is much greater than the ratio of samples to features available in our dataset. (B) The total number of samples required (nreq)) for a stable CCA solution given the total number of neural and symptom features used in our analyses, at different values of rtrue. In general these required sample sizes are much greater than the N=436 (light grey line) PSD in our present dataset, consistent with the finding that the CCA solutions computed using our data were unstable. Notably, the ‘12 vs. 5’ CCA assuming rtrue = 0.3 requires only 700 subjects, which is closest to the N=436 (horizontal grey line) used in the present sample. This may be in line with the observation of the CCA with 12 neural vs 5 symptom features (Fig. S15C) that the canonical correlation (r = 0.38 for CV1) clearly exceeds the 95% confidence interval, and may be closer to the true effect. However, to confidently detect effects in such an analysis (particularly if rtrue is actually less than 0.3), a larger sample would likely still be needed.

We also added the corresponding methods in the Methods section:

Multivariate CCA Power Analysis. Multivariate power analyses to estimate the minimum sample size needed to sufficiently power a CCA were computed using methods described in (3), using the Genera- tive Modeling of Multivariate Relationships tool (gemmr, https://github.com/murraylab/ gemmr (v0.1.2)). Briefly, a model was built by: 1) Generating synthetic datasets for the two input data matrices, by sampling from a multivariate normal distribution with a joint covariance matrix that was structured to encode CCA solutions with specified properties; 2) Performing CCAs on these synthetic datasets. Because the joint covariance matrix is known, the true values of estimated association strength, weights, scores, and loadings of the CCA, as well as the errors for these four metrics, can also be computed. In addition, statistical power that the estimated association strength is different from 0 is determined through permutation testing; 3) Varying parameters of the generative model (number of features, assumed true between-set correlation, within-set variance structure for both datasets) the required sample size Nreq is determined in each case such that statistical power reaches 90% and all of the above described error metrics fall to a target level of 10%; and 4) Fitting and validating a linear model to predict the required sample size Nreq from parameters of the generative model. This linear model was then used to calculate Nreq for CCA in three data scenarios: i) 718 neural vs. 5 symptom features; ii) 180 neural vs. 5 symptom features; iii) 12 neural vs. 5 symptom features.

• Given the relatively even distribution of males and females in the dataset, some examination of sex effects on symptom dimension loadings or neuro-behavioural maps would have been interesting (other demographic characteristics like age and SES are summarized for subjects but also not investigated). I think this is a missed opportunity.

We have now provided additional analyses for the core PCA and univariate GBC mapping results, testing for effects of age, sex, and SES in Fig. S8. Briefly, we observed a significant positive relationship between age and PC3 scores, which may be because older patients (whom presumably have been ill for a longer time) exhibit more severe symptoms along the positive PC3 – Psychosis Configuration dimension. We also observed a significant negative relationship between Hollingshead index of SES and PC1 and PC2 scores. Lower PC1 and PC2 scores indicate poorer general functioning and cognitive performance respectively, which is consistent with higher Hollingshead indices (i.e. lower-skilled jobs or unemployment and fewer years of education). We also found significant sex differences in PC2 – Cognitive Functioning, PC4 – Affective Valence, and PC5 – Agitation/Excitement scores.

Fig. S8. Effects of age, socio-economic status, and sex on symptom PCA solution. (A) Correlations between symptom PC scores and age (years) across N=436 PSD. Pearson’s correlation value and uncorrected p-values are reported above scatterplots. After Bonferroni correction, we observed a significant positive relationship between age and PC3 score. This may be because older patients have been ill for a longer period of time and exhibit more severe symptoms along the positive PC3 dimension. (B) Correlations between symptom PC scores and socio-economic status (SES) as measured by the Hollingshead Index of Social Position (31), across N=387 PSD with available data. The index is computed as (Hollingshead occupation score * 7) + (Hollingshead education score * 4); a higher score indicates lower SES (32). We observed a significant negative relationship between Hollingshead index and PC1 and PC2 scores. Lower PC1 and PC2 scores indicate poorer general functioning and cognitive performance respectively, which is consistent with higher Hollingshead indices (i.e. lower-skilled jobs or unemployment and fewer years of education). (C) The Hollingshead index can be split into five classes, with 1 being the highest and 5 being the lowest SES class (31). Consistent with (B) we found a significant difference between the classes after Bonferroni correction for PC1 and PC2 scores. (D) Distributions of PC scores across Hollingshead SES classes show the overlap in scores. White lines indicate the mean score in each class. (E) Differences in PC scores between (M)ale and (F)emale PSD subjects. We found a significant difference between sexes in PC2 – Cognitive Functioning, PC4 – Affective Valence, and PC5 – Agitation/Excitement scores. (F) Distributions of PC scores across M and F subjects show the overlap in scores. White lines indicate the mean score for each sex.

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Author Response

Reviewer #1 (Public Review):

Buglak et al. describe a role for the nuclear envelope protein Sun1 in endothelial mechanotransduction and vascular development. The study provides a full mechanistic investigation of how Sun1 is achieving its function, which supports the concept that nuclear anchoring is important for proper mechanosensing and junctional organization. The experiments have been well designed and were quantified based on independent experiments. The experiments are convincing and of high quality and include Sun1 depletion in endothelial cell cultures, zebrafish, and in endothelial-specific inducible knockouts in mice.

We thank the reviewer for their enthusiastic comments and for noting our use of multiple model systems.

Reviewer #2 (Public Review):

Endothelial cells mediate the growth of the vascular system but they also need to prevent vascular leakage, which involves interactions with neighboring endothelial cells (ECs) through junctional protein complexes. Buglak et al. report that the EC nucleus controls the function of cell-cell junctions through the nuclear envelope-associated proteins SUN1 and Nesprin-1. They argue that SUN1 controls microtubule dynamics and junctional stability through the RhoA activator GEF-H1.

In my view, this study is interesting and addresses an important but very little-studied question, namely the link between the EC nucleus and cell junctions in the periphery. The study has also made use of different model systems, i.e. genetically modified mice, zebrafish, and cultured endothelial cells, which confirms certain findings and utilizes the specific advantages of each model system. A weakness is that some important controls are missing. In addition, the evidence for the proposed molecular mechanism should be strengthened.

We thank the reviewer for their interest in our work and for highlighting the relative lack of information regarding connections between the EC nucleus and cell periphery, and for noting our use of multiple model systems. We thank the reviewer for suggesting additional controls and mechanistic support, and we have made the revisions described below.

Specific comments:

1) Data showing the efficiency of Sun1 inactivation in the murine endothelial cells is lacking. It would be best to see what is happening on the protein level, but it would already help a great deal if the authors could show a reduction of the transcript in sorted ECs. The excision of a DNA fragment shown in the lung (Fig. 1-suppl. 1C) is not quantitative at all. In addition, the gel has been run way too short so it is impossible to even estimate the size of the DNA fragment.

We agree that the DNA excision is not sufficient to demonstrate excision efficiency. We attempted examination of SUN1 protein levels in mutant retinas via immunofluorescence, but to date we have not found a SUN1 antibody that works in mouse retinal explants. We argue that mouse EC isolation protocols enrich but don’t give 100% purity, so that RNA analysis of lung tissue also has caveats. Finally, we contend that our demonstration of a consistent vascular phenotype in Sun1iECKO mutant retinas argues that excision has occurred. To test the efficiency of our excision protocol, we bred Cdh5CreERT2 mice with the ROSAmT/mG excision reporter (cells express tdTomato absent Cre activity and express GFP upon Cre-mediated excision (Muzumdar et al., 2007). Utilizing the same excision protocol as used for the Sun1iECKO mice, we see a significantly high level of excision in retinal vessels only in the presence of Cdh5CreERT2 (Reviewer Figure 1).

Reviewer Figure 1: Cdh5CreERT2 efficiently excises in endothelial cells of the mouse postnatal retina. (A) Representative images of P7 mouse retinas with the indicated genotypes, stained for ERG (white, nucleus). tdTomato (magenta) is expressed in cells that have not undergone Cre-mediated excision, while GFP (green) is expressed in excised cells. Scale bar, 100μm. (B) Quantification of tdTomato fluorescence relative to GFP fluorescence as shown in A. tdTomato and GFP fluorescence of endothelial cells was measured by creating a mask of the ERG channel. n=3 mice per genotype. ***, p<0.001 by student’s two-tailed unpaired t-test.

2) The authors show an increase in vessel density in the periphery of the growing Sun1 mutant retinal vasculature. It would be important to add staining with a marker labelling EC nuclei (e.g. Erg) because higher vessel density might reflect changes in cell size/shape or number, which has also implications for the appearance of cell-cell junctions. More ECs crowded within a small area are likely to have more complicated junctions. Furthermore, it would be useful and straightforward to assess EC proliferation, which is mentioned later in the experiments with cultured ECs but has not been addressed in the in vivo part.

We concur that ERG staining is important to show any changes in nuclear shape or cell density in the post-natal retina. We now include this data in Figure1-figure supplement 1F-G. We do not see obvious changes in nuclear shape or number, though we do observe some crowding in Sun1iECKO retinas, consistent with increased density. However, when normalized to total vessel area, we do not observe a significant difference in the nuclear signal density in Sun1iECKO mutant retinas relative to controls.

3) It appears that the loss of Sun1/sun1b in mice and zebrafish is compatible with major aspects of vascular growth and leads to changes in filopodia dynamics and vascular permeability (during development) without severe and lasting disruption of the EC network. It would be helpful to know whether the loss-of-function mutants can ultimately form a normal vascular network in the retina and trunk, respectively. It might be sufficient to mention this in the text.

We thank the reviewer for pointing this out. It is true that developmental defects in the vasculature resulting from various genetic mutations are often resolved over time. We’ve made text changes to discuss viability of Sun1 global KO mice and lack of perduring effects in sun1 morphant fish, perhaps resulting from compensation by SUN2, which is partially functionally redundant with SUN1 in vivo (Lei et al., 2009; Zhang, et al., 2009) (p. 20).

4) The only readout after the rescue of the SUN1 knockdown by GEF-H1 depletion is the appearance of VE-cadherin+ junctions (Fig. 6G and H). This is insufficient evidence for a relatively strong conclusion. The authors should at least look at microtubules. They might also want to consider the activation status of RhoA as a good biochemical readout. It is argued that RhoA activity goes up (see Fig. 7C) but there is no data supporting this conclusion. It is also not clear whether "diffuse" GEF-H1 localization translates into increased Rho A activity, as is suggested by the Rho kinase inhibition experiment. GEF-H1 levels in the Western blot in (Fig. 6- supplement 2C) have not been quantitated.

We agree that analysis of RhoA activity and additional analysis of rescued junctions strengthens our conclusions, so we performed these experiments. New data (Figure 6IJ) shows that co-depletion of SUN1 and GEF-H1 rescues junction integrity as measured by biotin-matrix labeling. Interestingly, co-depletion of SUN1 and GEF-H1 does not rescue reduced microtubule density at the periphery (Figure 6-figure supplement 3BC), placing GEF-H1 downstream of aberrant microtubule dynamics in SUN1 depleted cells. This is consistent with our model (Figure 8) describing how loss of SUN1 leads to increased microtubule depolymerization, resulting in release and activation of GEF-H1 that goes on to affect actomyosin contractility and junction integrity. In addition, we include images of the junctions in GEF-H1 single KD (Figure 6-figure supplement 3BC) and quantify the western blot in Figure 6-figure supplement 3A.

We performed RhoA activity assays and new data shows that SUN1 depletion results in increased RhoA activation, while co-depletion of SUN1 and GEF-H1 ameliorates this increase (Figure 6-figure supplement 2D). This is consistent with our model in which loss of SUN1 leads to increased RhoA activity via release of GEF-H1 from microtubules. In addition, we now cite a recent study describing that GEF-H1 is activated when unbound to microtubules, with this activation resulting in increased RhoA activity (Azoitei et al., 2019).

5) The criticism raised for the GEF-H1 rescue also applies to the co-depletion of SUN1 and Nesprin-1. This mechanistic aspect is currently somewhat weak and should be strengthened. Again, Rho A activity might be a useful and quantitative biochemical readout.

We respectfully point out that we showed that co-depletion of nesprin-1 and SUN1 rescues SUN1 knockdown effects via several readouts, including rescue of junction morphology, biotin labeling, microtubule localization at the periphery, and GEFH1/microtubule localization. We’ve moved this data to the main figure (Figure 7B-C, E-F) to better highlight these mechanistic findings. These results are consistent with our model that nesprin-1 effects are upstream of GEF-H1 localization. We also added results showing that nesprin-1 knockdown alone does not affect junction integrity, microtubule density, or GEF-H1/microtubule localization (Figure 7-figure supplement 1B-G).

Reviewer #3 (Public Review):

Here, Buglak and coauthors describe the effect of Sun1 deficiency on endothelial junctions. Sun1 is a component of the LINC complex, connecting the inner nuclear membrane with the cytoskeleton. The authors show that in the absence of Sun1, the morphology of the endothelial adherens junction protein VE-cadherin is altered, indicative of increased internalization of VE-cadherin. The change in VE-cadherin dynamics correlates with decreased angiogenic sprouting as shown using in vivo and in vitro models. The study would benefit from a stricter presentation of the data and needs additional controls in certain analyses.

We thank the reviewer for their insightful comments, and in response we have performed the revisions described below.

1) The authors implicate the changes in VE-cadherin morphology to be of consequence for "barrier function" and mention barrier function frequently throughout the text, for example in the heading on page 12: "SUN1 stabilizes endothelial cell-cell junctions and regulates barrier function". The concept of "barrier" implies the ability of endothelial cells to restrict the passage of molecules and cells across the vessel wall. This is tested only marginally (Suppl Fig 1F) and these data are not quantified. Increased leakage of 10kDa dextran in a P6-7 Sun1-deficient retina as shown here probably reflects the increased immaturity of the Sun1-deficient retinal vasculature. From these data, the authors cannot state that Sun1 regulates the barrier or barrier function (unclear what exactly the authors refer to when they make a distinction between the barrier as such on the one hand and barrier function on the other). The authors can, if they do more experiments, state that loss of Sun1 leads to increased leakage in the early postnatal stages in the retina. However, if they wish to characterize the vascular barrier, there is a wide range of other tissue that should be tested, in the presence and absence of disease. Moreover, a regulatory role for Sun1 would imply that Sun1 normally, possibly through changes in its expression levels, would modulate the barrier properties to allow more or less leakage in different circumstances. However, no such data are shown. The authors would need to go through their paper and remove statements regarding the regulation of the barrier and barrier function since these are conclusions that lack foundation.

We thank the reviewer for pointing out that the language used regarding the function and integrity of the junctions is confusing, although we suggest that the endothelial cell properties measured by our assays are typically equated with “barrier function” in the literature. However, we have edited our language to precisely describe our results as suggested by the reviewer.

2) In Fig 6g, the authors show that "depletion of GEF-H1 in endothelial cells that were also depleted for SUN1 rescued the destabilized cell-cell junctions observed with SUN1 KD alone". However, it is quite clear that Sun1 depletion also affects cell shape and cell alignment and this is not rescued by GEF-H1 depletion (Fig 6g). This should be described and commented on. Moreover please show the effects of GEF-H1 alone.

We thank the reviewer for pointing out the effects on cell shape. SUN1 depletion typically leads to shape changes consistent with elevated contractility, but this is considered to be downstream of the effects quantified here. We updated the panel in Figure 6G to a more representative image showing cell shape rescue by co-depletion of SUN1 and GEF-H1. We present new data panels showing that GEF-H1 depletion alone does not affect junction integrity (Figure 6I-J). We also present new data showing that co-depletion of GEF-H1 and SUN1 does not rescue microtubule density at the periphery (Figure 6-figure supplement 3B-C), consistent with our model that GEF-H1 activation is downstream of microtubule perturbations induced by SUN1 loss.

3) In Fig. 6a, the authors show rescue of junction morphology in Sun1-depleted cells by deletion of Nesprin1. The effect of Nesprin1 KD alone is missing.

We thank the reviewer for this comment, and we now include new panels (Figure 7figure supplement 1B-G) demonstrating that Nesprin-1 depletion does not affect biotin-matrix labeling, peripheral microtubule density, or GEF-H1/microtubule localization absent co-depletion with SUN1. These findings are consistent with our model that Nesprin-1 loss does not affect cell junctions on its own because it is held in a non-functional complex with SUN1 that is not available in the absence of SUN1.

References

Azoitei, M. L., Noh, J., Marston, D. J., Roudot, P., Marshall, C. B., Daugird, T. A., Lisanza, S. L., Sandί, M., Ikura, M., Sondek, J., Rottapel, R., Hahn, K. M., Danuser, & Danuser, G. (2019). Spatiotemporal dynamics of GEF-H1 activation controlled by microtubule- and Src-mediated pathways. Journal of Cell Biology, 218(9), 3077-3097. https://doi.org/10.1083/jcb.201812073

Denis, K. B., Cabe, J. I., Danielsson, B. E., Tieu, K. V, Mayer, C. R., & Conway, D. E. (2021). The LINC complex is required for endothelial cell adhesion and adaptation to shear stress and cyclic stretch. Molecular Biology of the Cell, mbcE20110698. https://doi.org/10.1091/mbc.E20-11-0698

King, S. J., Nowak, K., Suryavanshi, N., Holt, I., Shanahan, C. M., & Ridley, A. J. (2014). Nesprin-1 and nesprin-2 regulate endothelial cell shape and migration. Cytoskeleton (Hoboken, N.J.), 71(7), 423–434. https://doi.org/10.1002/cm.21182

Lei, K., Zhang, X., Ding, X., Guo, X., Chen, M., Zhu, B., Xu, T., Zhuang, Y., Xu, R., & Han, M. (2009). SUN1 and SUN2 play critical but partially redundant roles in anchoring nuclei in skeletal muscle cells in mice. PNAS, 106(25), 10207–10212.

Muzumdar, M. D., Tasic, B., Miyamichi, K., Li, L., & Luo, L. (2007). A global doublefluorescent Cre reporter mouse. Genesis, 45(9), 593-605. https://doi.org/10.1002/dvg.20335

Ueda, N., Maekawa, M., Matsui, T. S., Deguchi, S., Takata, T., Katahira, J., Higashiyama, S., & Hieda, M. (2022). Inner Nuclear Membrane Protein, SUN1, is Required for Cytoskeletal Force Generation and Focal Adhesion Maturation. Frontiers in Cell and Developmental Biology, 10, 885859. https://doi.org/10.3389/fcell.2022.885859

Zhang, X., Lei, K., Yuan, X., Wu, X., Zhuang, Y., Xu, T., Xu, R., & Han, M. (2009). SUN1/2 and Syne/Nesprin-1/2 complexes connect centrosome to the nucleus during neurogenesis and neuronal migration in mice. Neuron, 64(2), 173–187. https://doi.org/10.1016/j.neuron.2009.08.018.

Author Response

Reviewer #1 (Public Review):

In Figure 1A, the authors should show TEM images of control mock treated samples to show the difference between infected and healthy tissue. Based on the data shown in Figure 1B-E that the overexpression of GFP-P in N. benthamiana leads to formation of liquid-like granules. Does this occur during virus infection? Since authors have infectious clones, can it be used to show that the virally encoded P protein in infected cells does indeed exist as liquid-like granules? If the fusion of GFP to P protein affects its function, the authors could fuse just the spGFP11 and co-infiltrate with p35S-spGFP1-10. These experiments will show that the P protein when delivered from virus does indeed form liquid-like granules in plants cells. Authors should include controls in Figure 1H to show that the interaction between P protein and ER is specific.

We agree with the reviewer and appreciate the helpful suggestion. As suggested, we added TEM images of control mock treated barley leaves. We also carried out immune-electron microscope to show the presence of BYSMV P protein in the viroplasms. Please see Figure 1–Figure supplement 1.

BYSMV is a negative-stranded RNA virus, and is strictly dependent on insect vector transmission for infecting barley plants. We have tried to fuse GFP to BYSMV P in the full-length infectious clones. Unfortunately, we could not rescue BYSMV-GFP-P into barley plants through insect transmission.

In Figure 1H, we used a PM localized membrane protein LRR84A as a negative control to show LRR84A-GS and BYSMV P could not form granules although they might associate at molecular distances. Therefore, the P granules were formed and tethered to the ER tubules. Please see Figure 1–Figure supplement 4

Data shown in Figure 2 do demonstrate that the purified P protein could undergo phase separation. Furthermore, it can recruit viral N protein and part of viral genomic RNA to P protein induced granules in vitro.

Because the full-length BYSMV RNA has 12,706 nt and is difficult to be transcribed in vitro, we cannot show whether the BYSMV genome is recruited into the droplets. We have softened the claim and state that the P-N droplets can recruit 5′ trailer of BYSMV genome as shown in Figure 3B. Please see line 22, 177 and 190.

Based on the data shown in Figure 4 using phospho-null and phospho-mimetic mutants of P protein, the authors conclude that phosphorylation inhibits P protein phase separation. It is unclear based on the experiments, why endogenous NbCK1 fails to phosphorylate GFP-P-WT and inhibit formation of liquid-like granules similar to that of GFP-P-S5D mutant? Is this due to overexpression of GFP-P-WT? To overcome this, the authors should perform these experiments as suggested above using infectious clones and these P protein mutants.

As we known, phosphorylation and dephosphorylation are reversible processes in eukaryotic cells. Therefore, as shown in Figure 5B and 6B, the GFP-PWT protein have two bands, corresponding to P74 and P72, which represent hyperphosphorylation and hypophosphorylated forms, respectively. Only overexpression of NbCK1 induced high ratio of P74 to P72 in vivo, and then abolished phase separation of BYSMV.

In Figure 5, the authors overexpress NbCK1 in N. benthamiana or use an in vitro co-purification scheme to show that NbCK1 inhibits phase separation properties of P protein. These results show that overexpression of both GFP-P and NbCK1 proteins is required to induce liquid-like granules. Does this occur during normal virus infection? During normal virus infection, P protein is produced in the plant cells and the endogenous NbCK1 will regulate the phosphorylation state of P protein. These are reasons for authors to perform some of the experiments using infectious clones. Furthermore, the authors have antibodies to P protein and this could be used to show the level of P protein that is produced during the normal infection process.

We detected the P protein existed as two phosphorylation forms in BYSMV-infected barley leaves, and λPPase treatment decreased the P44 phosphorylation form. Therefore, these results indicate that endogenous CK1 cannot phosphorylate BYSMV P completely.

Based on the data shown in Figure 6, the authors conclude that phase separated P protein state promotes replication but inhibits transcription by overexpressing P-S5A and P-S5D mutants. To directly show that the NbCK1 controlled phosphorylation state of P regulates this process, authors should knockdown/knockout NbCK1 and see if it increases P protein condensates and promote recruitment of viral proteins and genomic RNA to increase viral replication.

In our previous studies, BLAST searches showed that the N. benthamiana and barley genomes encode 14 CK1 orthologs, most of which can phosphorylated the SR region of BYSMV P. Therefore, it is difficult to make knockdown/knockout lines of all the CK1 orthologues. Accordingly, we generated a point mutant (K38R and D128N) in HvCK1.2, in which the kinase activity was abolished. Overexpression of HvCK1.2DN inhibit endogenous CK1-mediated phosphorylation of BYSMV P, indicating that HvCK1.2DN is a dominant-negative mutant.

It is important to note that both replication and transcription are required for efficient infection of negative-stranded RNA viruses. Therefore, our previous studies have revealed that both PS5A and PS5D are required for BYSMV infection. Therefore, expression of HvCK1.2DN in BYSMV vector inhibit virus infection by impairing the balance of endogenous CK1-mediated phosphorylation in BYSMV P.

Reviewer #2 (Public Review):

The manuscript by Fang et al. details the ability of the P protein from Barley yellow striate mosaic virus (BYSMV) to form phase-separated droplets both in vitro and in vivo. The authors demonstrate P droplet formation using recombinant proteins and confocal microscopy, FRAP to demonstrate fluidity, and observed droplet fusion. The authors also used an elaborate split-GFP system to demonstrate that P droplets associate with the tubulur ER network. Next, the authors demonstrate that the N protein and a short fragment of viral RNA can also partition into P droplets. Since Rhabdovirus P proteins have been shown to phase separate and form "virus factories" (see https://doi.org/10.1038/s41467-017-00102-9), the novelty from this work is the rigorous and conclusive demonstration that the P droplets only exist in the unphosphorylated form. The authors identify 5 critical serine residues in IDR2 of P protein that when hyper-phosphorylated /cannot form droplets. Next, the authors conclusively demonstrate that the host kinase CK1 is responsible for P phosphorylation using both transient assays in N. benthamiana and a co-expression assay in E. coli. These findings will likely lead to future studies identifying cellular kinases that affect phase separation of viral and cellular proteins and increases our understanding of regulation of condensate formation. Next, the authors investigated whether P droplets regulated virus replication and transcription using a minireplicon system. The minireplicon system needs to be better described as the results were seemingly conflicting. The authors also used a full-length GFP-reporter virus to test whether phase separation was critical for virus fitness in both barley and the insect vector. The authors used 1, 6-hexanediol which broadly suppresses liquid-liquid phase separation and concluded that phase separation is required for virus fitness (based on reduced virus accumulation with 1,6 HD). However, this conclusion is flawed since 1,6-hexanediol is known to cause cell toxicity and likely created a less favorable environment for virus replication, independent of P protein phase separation. These with other issues are detailed below:

1. In Figure 3B, the authors display three types of P-N droplets including uniform, N hollow, and P-N hollow droplets. The authors do not state the proportion of droplets observed or any potential significance of the three types. Finally, as "hollow" droplets are not typically observed, is there a possibility that a contaminating protein (not fluorescent) from E. coli is a resident client protein in these droplets? The protein purity was not >95% based on the SDS-PAGE gels presented in the supplementary figures. Do these abnormalities arise from the droplets being imaged in different focal planes? Unless some explanation is given for these observations, this reviewer does not see any significance in the findings pertaining to "hollow" droplets.

Thanks for your constructive suggestions. We removed the "hollow" droplets as suggested. We think that the hollow droplets might be an intermediate form of LLPS. Please see PAGE 7 and 8 of revised manuscript.

1. Pertaining to the sorting of "genomic" RNA into the P-N droplets, it is unlikely that RNA sorting is specific for BYSMV RNA. In other words, if you incubate a non-viral RNA with P-N droplets, is it sorted? The authors conclusion that genomic RNA is incorporated into droplets is misleading in a sense that a very small fragment of RNA was used. Cy5 can be incorporated into full-length genomic RNAs during in vitro transcription and would be a more suitable approach for the conclusions reached.

Thanks for your constructive suggestions. Unfortunately, we could not obtain the in vitro transcripts of the full-length genomic RNAs (12706 nucleotides). We have softened the claim and state that the P-N droplets can recruit the 5′ trailer of BYSMV genome as shown in Figure 3B. Please see line 22, 177 and 190.

According to previous studies (Ivanov, et al., 2011), the Rhabdovirus P protein can bind to nascent N moleculaes, forming a soluble N/P complex, to prevent from encapsidating cellular RNAs. Therefore, we suppose that the P-N droplets can incorporate viral genomic RNA specifically.

Reference: Ivanov I, Yabukarski F, Ruigrok RW, Jamin M. 2011. Structural insights into the rhabdovirus transcription/ replication complex. Virus Research 162:126–137. DOI: https://doi.org/10.1016/j.virusres.2011.09.025

1. In Figure 4C, it is unclear how the "views" were selected for granule counting. The methods should be better described as this reviewer would find it difficult to select fields of view in an unbiased manner. This is especially true as expression via agroinfiltration can vary between cells in agroinfiltrated regions. The methods described for granule counting and granule sizes are not suitable for publication. These should be expanded (i.e. what ImageJ tools were used?).

We agree with the reviewer that it is important to select fields of view in an unbiased manner. We selected the representative views and provided large views in the new Supplement Figures. In addition, we added new detail methods in revision. Please see Figure 4–Figure supplement 1, Figure 5–Figure supplement 1, and method (line 489-498).

1. In Figure 4F, the authors state that they expected P-S5A to only be present in the pellet fraction since it existed in the condensed state. However, WT P also forms condensates and was not found in the pellet, but rather exclusively in the supernatant. Therefore, the assumption of condensed droplets only being found in the pellet appears to be incorrect.

Many thanks for pointing this out. This method is based on a previous study (Hubstenberger et al., 2017). The centrifugation method might efficiently precipitate large granules more than small granules. As shown in Figure 4B, GFP-PS5A formed large granules, therefore GFP-PS5A mainly existed in the pellet. In contrast, GFP-PWT only existed in small granule and fusion state, thus most of GFP-PWT protein was existed in supernatant, and only little GFP-PWT protein in the pellet. These results also indicate the increased phase separation activity of GFP-PS5A compared with GFP-PWT. Please see the new Figure 4F.

Reference: Hubstenberger A, Courel M, Benard M, Souquere S, Ernoult-Lange M, Chouaib R, Yi Z, Morlot JB, Munier A, Fradet M, et al. 2017. P-Body Purification Reveals the Condensation of Repressed mRNA Regulons. Molecular Cell 68(1): 144-157 e145.

1. The authors conclude that P-S5A has enhanced phase separation based on confocal microscopy data (Fig S6A). The data presented is not convincing. Microscopy alone is difficult for comparing phase separation between two proteins. Quantitative data should be collected in the form of turbidity assays (a common assay for phase separation). If P-S5A has enhanced phase separation compared to WT, then S5A should have increased turbidity (OD600) under identical phase separation conditions. The microscopy data presented was not quantified in any way and the authors could have picked fields of view in a biased manner.

Thanks for your constructive suggestions. As suggested, turbidity assays were performed to show both GFP-PWT and GFP-PS5A had increased turbidity (OD600) compared with GFP. Please see Figure 4–Figure supplement 3.

1. The authors constructed minireplicons to determine whether mutant P proteins influence RNA replication using trans N and L proteins. However, this reviewer finds the minireplicon design confusing. How is DsRFP translated from the replicon? If a frameshift mutation was introduced into RsGFP, wouldn't this block DsRFP translation as well? Or is start/stop transcription used? Second, the use of the 2x35S promoter makes it difficult to differentiate between 35S-driven transcription and replication by L. How do you know the increased DsRFP observed with P5A is not due to increased transcription from the 35S promoter? The RT-qPCR data is also very confusing. It is not clear that panel D is only examining the transcription of RFP (I assume via start/stop transcription) whereas panel C is targeting the minireplicon.

Thank you for your questions and we are sorry for the lack of clarity regarding to the mini-replicon vectors. Here, we updated the Figure supplement 14 to show replication and transcription of BYSMV minireplicon, a negative-stranded RNA virus derivative. In addition, we insert an A after the start codon to abolish the translation of GFP mRNA, which allow us to observe phase separation of GFP-PWT, GFP-PS5A, and GFP-PS5D during virus replication. Use this system, we wanted to show the localization and phase separation of GFP-PWT, GFP-PS5A, and GFP-PS5D during replication and transcription of BYS-agMR. Please see Figure 6–Figure supplement 1.

1. Pertaining to the replication assay in Fig. 6, transcription of RFP mRNA was reduced by S5A and increased by S5D. However, the RFP translation (via Panel A microscopy) is reversed. How do you explain increased RFP mRNA transcription by S5D but very low RFP fluorescence? The data between Panels A, C, and D do not support one another.

Many thanks for pointing this out! We also noticed the interesting results that have been repeated independently. As shown the illustration of BYSMV-agMR system in Figure 6–Figure supplement 1, the relative transcriptional activities of different GFP-P mutants were calculated from the normalized RFP transcript levels relative to the gMR replicate template (RFP mRNA/gMR), because replicating minigenomes are templates for viral transcription.

Since GFP-PS5D supported decreased replication, the ratio of RFP mRNA/gMR increased although the RFP mRNA of GFP-PS5D is not increased. In addition, the foci number of GFP-PS5D is much less than GFP-PWT and GFP-PS5A, indicating mRNAs in GFP-PS5D samples may contain aberrant transcripts those cannot be translated the RFP protein. In contrast, mRNAs in GFP-PS5A samples are translated efficiently. These results were in consistent with our previous studies using the free PWT, PS5A, and PS5D.

Reference: Gao Q, et al. 2020. Casein kinase 1 regulates cytorhabdovirus replication and transcription by phosphorylating a phosphoprotein serine-rich motif. The Plant Cell 32(9): 2878-2897.

1. The authors relied on 1,6-hexanediol to suppress phase separation in both insect vectors and barley. However, the authors disregarded several publications demonstrating cellular toxicity by 1,6-hexanediol and a report that 1,6-HD impairs kinase and phosphatase activities (see below). doi: 10.1016/j.jbc.2021.100260,

We agree with the reviewer that 1, 6-hexanediol induced cellular toxicity. Therefore, we removed these results, which does not affect the main conclusion of our results.

1. The authors state that reduced accumulation of BYSMV-GFP in insects and barley under HEX treatment "indicate that phase separation is important for cross-kingdom infection of BYSMV in insect vectors and host plants." The above statement is confounded by many factors, the most obvious being that HEX treatment is most likely toxic to cells and as a result cannot support efficient virus accumulation. Also, since HEX treatment interferes with phosphorylation (see REF above) its use here should be avoided since P phase separation is regulated by phosphorylation.

We agree with the reviewer that 1, 6-hexanediol induced cellular toxicity and hereby affected infections of BYSMV and other viruses. In addition, 1, 6-hexanediol would inhibit LLPS of cellular membraneless organelles, such as P-bodies, stress granules, cajal bodies, and the nucleolus, which also affect different virus infections directly or indirectly. Therefore, we removed these results, which does not affect the main conclusion of our results.

Reviewer #3 (Public Review):

Membrane-less organelles formed through liquid-liquid phase separation (LLPS) provide spatiotemporal control of host immunity responses and other cellular processes. Viruses are obligate pathogens proliferating in host cells which lead their RNAs and proteins are more likely to be targeted by immune-related membrane-less organelles. To successfully infect and proliferate in host cells, virus need to efficiently suppressing the immune function of those immune-related membrane-less organelles. Moreover, viruses also generate exogenous membrane-less organelles/RNA granules to facilitate their proliferation. Accordingly, host cells also need to target and suppress the functions of exogenous membrane-less organelles/RNA granules generated by viruses, the underlying mechanisms of which are still mysterious.

In this study, Fang et al. investigated how plant kinase confers resistance against viruses via modulating the phosphorylation and phase separation of BYSMV P protein. They firstly characterized the phase separation feature of BYSMV P protein. They also discovered that droplets formed by P protein recruit viral RNA and other viral protein in vivo. The phase separation activity of P protein is inhibited by the phosphorylation on its intrinsically disordered region. Combined with their previous study, this study demonstrated that host casein kinase (CK1) decreases the phase separation of P protein via increasing the phosphorylation of P protein. Finally, the author claimed that the phase separation of P protein facilitates BYSMV replication but decreases its transcription. Taking together, this study uncovered the molecular mechanism of plant regulating viral proliferation via decreasing the formation of exogenous RNA granules/membraneless organelles. Overall, this paper tells an interesting story about the host immunity targeting viruses via modulating the dynamics of exogenous membraneless organelles, and uncovers the modulation of viral protein phase separation by host protein, which is a hotspot in plant immunity, and the writing is logical.

Thanks for your positive comment on our studies.

Author Response:

Reviewer #1 (Public Review):

Here the authors use a variety of sophisticated approaches to assess the contribution of synaptic parameters to dendritic integration across neuronal maturation. They provide high-quality data identifying cellular parameters that underlie differences in AMPAR-mediated synaptic currents measured between adolescent and adult cerebellar stellate cells, and conclude that differences are attributed to an increase in the complexity of the dendritic arbor. This conclusion relies primarily on the ability of a previously described model for adult stellate cells to recapitulate the age-dependent changes in EPSCs by a change in dendritic branching with no change in synapse density. These rigorous results have implications for understanding how changing structure during neuronal development affects integration of AMPR-mediated synaptic responses.

The data showing that younger SCs have smaller dendritic arbors but similar synapse density is well-documented and provides compelling evidence that these structural changes affect dendritic integration. But the main conclusion also relies on the assumption that the biophysical model built for adult SCs applies to adolescent SCs, and there are additional relevant variables related to synaptic function that have not been fully assessed. Thus, the main conclusions would be strengthened and broadened by additional experimental validation.

We thank the reviewer for the positive assessment of the quality and importance of our manuscript. Below we address the reviewer’s comments directly but would like to stress that the goal of the manuscript was to understand the cellular mechanisms underlying developmental slowing of mEPSCs in SCs and the consequent implication for developmental changes in dendritic integration, which have rarely been examined to date, and not to establish a detailed biophysical model of cerebellar SCs. The latter would require dual-electrode recordings (one on 0.5 um dendrites), detailed description of the expression, dendritic localization of the gap junction protein connexin 36 (as done in Szoboszlay neuron 2016), and a detailed description prameter variability across the SC population (e.g. variations in AMPAR content at synapses, Rm, and dendritic morphology). Such experiments are well beyond the scope of the manuscript. Here we use biophysical simulations to support conclusions derived from specific experiments, more as a proof of principle rather than a strict quantitative prediction.

Nevertheless, we would like to clarify our selection of parameters for the biophysical models for immature and adult SCs. We did not simply “assume” that the biophysical models were the same at the two developmental stages. We either used evidence from the literature or our own measured parameters to establish an immature SC model. As compared to adult SCs, we found that immature SCs had 1) an identical membrane time constant, 2) an only slightly larger dendrite diameter, 3) decreased dendritic branching and maximum lengths, 4) a comparable synapse density, and 5) a homogeneous synapse distribution. Taken together, we concluded that increased dendritic branching during SC maturation resulted in a larger fraction of synapses at longer electrotonic distances in adult SCs. These experimental findings were incorporated into two distinct biophysical models representing immature and adult SCs. Evidence from the literature suggests that voltage-gated channels expression is not altered between the two developmental stages studied here. Therefore, like the adult SC model, we considered only the passive membrane properties and the dendritic morphology. The simulation results supported our conclusion that the increased apparent dendritic filtering of mEPSCs resulted from a change in the distribution of synapse distance to the soma rather than cable properties. Some of the measured parameters (e.g., membrane time constant) were not clearly stated manuscript, which we have corrected in the revised manuscript.

We are not sure what the reviewer meant by suggesting that we did not examine “other relevant variables related to synaptic function.” Later, the reviewer refers to alterations in AMPAR subunit composition or changes in cleft glutamate concentration (low-affinity AMPAR antagonist experiments). We performed experiments to directly examine both possible contributions by comparing qEPSC kinetics and performing low-affinity antagonist experiments, respectively, but we found that neither mechanism could account for the developmental slowing of mEPSCs. We, therefore, did not explore further possible developmental changes AMPAR subunits. See below for a more specific response and above for newly added text.

While many exciting questions could be examined in the future, we do not think the present study requires additional experiments. Nevertheless, we recognize that perhaps we can improve the description of the results to justify our conclusions better (see specifics below).

Reviewer #2 (Public Review):

This manuscript investigates the cellular mechanisms underlying the maturation of synaptic integration in molecular layer interneurons in the cerebellar cortex. The authors use an impressive combination of techniques to address this question: patch-clamp recordings, 2-photon and electron microscopy, and compartmental modelling. The study builds conceptually and technically on previous work by these authors (Abrahamsson et al. 2012) and extends the principles described in that paper to investigate how developmental changes in dendritic morphology, synapse distribution and strength combine to determine the impact of synaptic inputs at the soma.

1) Models are constructed to confirm the interpretation of experimental results, mostly repeating the simulations from Abrahamsson et al. (2012) using 3D reconstructed morphologies. The results are as expected from cable theory, given the (passive) model assumptions. While this confirmation is welcome and important, it is disappointing to see the opportunity missed to explore the implications of the experimental findings in greater detail. For instance, with the observed distributions of synapses, are there more segregated subunits available for computation in adult vs immature neurons?

As described in our response to reviewer 1, this manuscript intends to identify the cellular mechanisms accounting developmental slowing of mEPSCs and its implication for dendritic integration. The modeling was designed to support the most plausible explanation that increased branching resulted in more synapses at longer electrotonic distances. This finding is novel and merits more in-depth examination at a computation level in future studies.

Quantifying dendritic segregation is non-trivial due to dendritic nonlinearities and the difficulties in setting criteria for electrical “isolation” of inputs. However, because the space constant does not change with development, while both dendrite length and branching increase, it is rather logical to conclude qualitatively that the number of computational segments increases with development.

We have added the following sentence to the Discussion (line 579):

“Moreover, since the space constant does not change significantly with development and the dendritic tree complexity increases, the number of computational segments is expected to increase with development.”

How do SCs respond at different developmental stages with in vivo-like patterns of input, rather than isolated activation of synapses? Answering these sorts of questions would provide quantitative support for the conclusion that computational properties evolve with development.

While this is indeed a vital question, the in vivo patterns of synaptic activity are not known, so it is difficult to devise experiments to arrive at definitive conclusions.

2) From a technical perspective, the modeling appears to be well-executed, though more methodological detail is required for it to be reproducible. The AMPA receptor model and reversal potential are unspecified, as is the procedure for fitting the kinetics to data.

We did not use an explicit channel model to generate synaptic conductances. We simply used the default multiexponential function of Neuron (single exponential rise and single exponential decay) and adjusted the parameters tauRise and tauDecay such that simulated EPSCs matched somatic quantal EPSC amplitude, rise time and τdecay (Figure 4).

We added the following text to the methods (line 708):

“The peak and kinetics of the AMPAR-mediated synaptic conductance waveforms (gsyn) were set to simulate qEPSCs that matched the amplitude and kinetics of experimental somatic quantal EPSCs and evoked EPSCs. Immature quantal gsyn had an peak amplitude of 0.00175 μS, a 10-90 % RT of 0.0748 ms and a half-width of 0.36 ms (NEURON synaptic conductance parameter Tau0 = 0.073 ms, Tau1 = 0.26 ms and Gmax = 0.004 μS) while mature quantal gsyn had an peak amplitude of 0.00133 μS, a 10-90 % RT of 0.072 ms and a half-width of 0.341 ms (NEURON synaptic conductance parameters Tau0 = 0.072 ms, Tau1 = 0.24 ms and Gmax = 0.0032 μS). For all simulations, the reversal potential was set to 0 mV and the holing membrane potential was to – 70 mV. Experimental somatic PPR for EPSCs were reproduced with a gsyn 2/ gsyn 1 of 2.25.”

Were simulations performed at resting potential, and if yes, what was the value?

The membrane potential was set at – 70 mV to match that of experimental recordings and has been updated in the Methods section.

How was the quality of the morphological reconstructions assessed? Accurate measurement of dendritic diameters is crucial to the simulations in this study, so providing additional morphometrics would be helpful for assessing the results. Will the models and morphologies be deposited in ModelDB or similar?

For the two reconstructions imported into NEURON for simulations, we manually curated the dendritic diameters to verify a matching of the estimated diameter to that of the fluorescence image using NeuroStudio, which uses a robust subpixel estimation algorithm (Rayburst diameter, Rodriguez et al. 2008). The reconstructions include all variations in diameter throughout the dendritic tree (see as a example the the result of the reconstruction on the image below for the immature SC presented in the Figure 2D). The mean diameter across the entire dendritic tree of the reconstructed immature and adult SC was 0.42 and 0.36 μm, respectively, similar to the ratio of measured diameters estimated using confocal microscopy.

We have updated the methods section to include how reconstructions were curated and analyzed (line 693).

“An immature (P16) and adult SC (P42) were patch loaded with 30 μM Alexa 594 in the pipette and imaged using 2PLSM. Both cells were reconstructed in 3D using NeuronStudio in a semiautomatic mode which uses a robust subpixel estimation algorithm (calculation of Rayburst diameter (Rodriguez et al., 2008)). We manually curated the diameters to verify that it matched the fluorescence image to faithfully account for all variations in diameter throughout the dendritic tree. The measured diameter across the entire dendritic tree of the reconstructed immature and adult SCs was 0.42 and 0.36 μm, respectively. The 16% smaller diameter in adult was similar to the 13% obtained from confocal image analysis from many SCs (see Figure 2B).”

We agree with the reviewer that accurate measurements of dendritic diameters are crucial for the simulations. We did not rely soley on the reconstructed SCs, but we also performed highresolution confocal microscopy analysis of 16 different dye-filled SCs. We examined differences in the FWHM of intensity line profiles drawn perpendicular to the dendrite between immature and adult SCs. The FWHM is a good approximation of dendritic diameter and was performed similarly to adult SCs (Abrahamsson et al., 2012) to allow direct assessment of possible developmental differences. We confirmed that 98% of the estimated diameters are larger than the imaging resolution (0.27 μm). We observed only a small developmental difference in the mean FWHM (0.41 vs. 0.47 μm, 13% reduction) using this approach. Because the dendritic filtering is similar for diameters ranging from 0.3 to 0.6 μm (Figure 4G and 4H, Abrahamsson et al. 2012), we concluded that developmental changes in dendritic diameter cannot account for for developmental differences in mEPSC time course.

We added the following text to the methods (line 777):

“The imaging resolution within the molecular layer was estimated from the width of intensity line profiles of SC axons. The FWHM was 0.30 +/- 0.01 μm (n = 57 measurements over 16 axons) and a mean of 0.27 +/- 0.01 μm (n = 16) when taking into account the thinnest section for each axon. Only 2% of all dendritic measurements are less than 270 nm, suggesting that the dendritic diameter estimation is hardly affected by the resolution of our microscope”

Regarding additional morphometrics:

1) We added two panels (H and I) to Figure 6 showing the number of primary dendrites and branch points for immature and adult using the same estimation criteria as Myoga et al;, 2009. We have updated the Results section (line 389). “Thus, the larger number of puncta located further from the soma in adult SCs is not due to increased puncta density with distance, but a larger dendritic lengths (Figure 6E and 6F) and many more distal dendritic branches (Figure 6G, Sholl analysis) due to a larger number of branch points (Figure 6H), but not a larger number of primary dendrites (Figure 6I). The similarity between the shapes of synapse (Figure 6B) and dentric segment (Figure 6C) distributions was captured by a similarity in their skewness (0.38 vs. 0.32 for both distributions in immature and -0.10 and -0.08 for adult distributions). These data demonstrate that increased dendritic complexity during SC maturation is responsible for a prominent shift toward distal synapses in adult SCs.

2) As suggested by the reviewer, we estimated the dendritic width as a function branch order and observed a small reduction of dendritic segments as a function of distance from the soma that does not significantly alter the dendritic filtering (0.35 to 0.6 μm): there is a tendency to observe smaller diameter for more distal segments.

3) We also show the variability in dendritic diameter within single SCs and between different SCs, which can be very large. These results have been added to Figure 2B. See also point one below in response to “comment to authors.”

We will upload the two SC reconstructions to ModelDB.

3) The Discussion should justify the assumption of AMPA-only synapses in the model (by citing available experimental data) as well as the limitations of this assumption in the case of different spatiotemporal patterns of parallel fiber activation.

NMDARs are extrasynaptic in immature and adult SCs. Therefore they do not contribute to postsynaptic strength in response to low-frequency synaptic activation. We therefore do not consider their contribution to synaptic integration in this study. Please see also out detailed response to reviewer’s point 4. We have updated the Results accordingly.

4) What is the likely influence of gap junction coupling between SCs on the results presented here, and on synaptic integration in SCs more generally - and how does it change during development? This should also be discussed.

Please see a detailed response to Editor’s point 2. In brief, all recordings were performed without perturbing gap junction coupling between cells, which have been shown to affect axial resistance and membrane capacitance in other cell types (Szoboszlay et al., 2016). While our simulations do not explicitly include gap junctions, their effect on passive membrane properties is implicitly included because we matched the simulated membrane time constant to experimental values. Moreover, gap junctions are more prominent in cerebellar basket cells than SCs in both p18 to p21 animals (Rieubland 2015) and adult mice (Hoehne et al., 2020). Ultimately, the impact of gap junctions also depends on their distance from the activated synapses (Szoboszlay et al., 2016). Unfortunately, the distribution of gap junctions in SCs and their conductance is not known at this time. We, therefore, did not explicitly consider gap junction in this study.

Nevertheless, we have added a section in the Discussion (line 552):

“We cannot rule out that developmental changes in gap junction expression could contribute to the maturation of SC dendritic integration, since they are thought to contribute to the axial resistivity and capacitance of neurons (Szoboszlay et al., 2016). All the recordings were made with gap junctions intact, including for membrane time constant measurements. However, their expression in SCs is likely to be lower than their basket cell counterparts (Hoehne et al., 2020; Rieubland et al., 2014).”

5) All experiments and all simulations in the manuscript were done in voltage clamp (the Methods section should give further details, including the series resistance). What is the significance of the key results of the manuscript on synapse distribution and branching pattern of postsynaptic dendrites in immature and adult SCs for the typical mode of synaptic integration in vivo, i.e. in current clamp? What is their significance for neuronal output, considering that SCs are spontaneously active?

It should be noted that not all simulations were done in voltage-clamp, see figure 8.

Nevertheless, we have given additional details about the following experimental and simulation parameters:

1) Description of the whole-cell voltage-clamp procedure.

2) Series resistance values of experiments and used for simulations.

Initial simulations with the idealized SC model were performed with a Rs of 20 MOhm. In the reconstructed model Rs was set at 16 mOhm to match more precisely the experimental values obtained for the mEPSC experiments. We verified that there were no statistical difference in Rs between Immature and adult recordings.

Reviewer #3 (Public Review):

1) Although the authors were thorough in their efforts to find the mechanism underlying the differences in the young and adult SC synaptic event time course, the authors should consider the possibility of inherently different glutamate receptors, either by alterations in the subunit composition or by an additional modulatory subunit. The literature actually suggests that this might be the case, as several publications described altered AMPA receptor properties (not just density) during development in stellate cells (Bureau, Mulle 2004; Sun, Liu 2007; Liu, Cull-Candy 2002). The authors need to address these possibilities, as modulatory subunits are known to alter receptor kinetics and conductance as well.

Properties of synaptic AMPAR in SCs are known to change during development and in an activity-dependent manner. EPSCs in immature SC have been shown to be mediated by calcium permeable AMPARs, predominantly containing GluR3 subunits that are associated with TARP γ2 and γ7 (Soto et al. 2007; Bats et al., 2012). During development GluR2 subunits are inserted to the synaptic AMPAR in an activity-dependent manner (Liu et al, 2000), affecting the receptors’ calcium permeability (Liu et al., 2002). However, those developmental changes do not appear to affect EPSC kinetics (Liu et al., 2002) and have very little impact on AMPAR conductance (Soto et al., 2007). When we compare qEPSC kinetics for somatic synapses between immature and adult SC, we did not observe changes in EPSC decay. In the light of this observation and also consistent with the studies cited above, we concluded that differences in AMPAR composition could not contribute to kinetics differences observed in the developmental changes in mEPSC properties.

We have modified the manuscript to make this point clearer (see section starting line 332) :

“This reduction in synaptic conductance could be due to a reduction in the number of synaptic AMPARs activated and/or a developmental change in AMPAR subunits. SC synaptic AMPARs are composed of GluA2 and GluA3 subunits associated with TARP γ2 and γ7 (Bats et al., 2012; Liu and Cull-Candy, 2000; Soto et al., 2007; Yamazaki et al., 2015). During development, GluR2 subunits are inserted to the synaptic AMPAR in an activity-dependent manner (Liu and Cull-Candy, 2002), affecting receptors calcium permeability (Liu and Cull-Candy, 2000). However, those developmental changes have little impact on AMPAR conductance (Soto et al., 2007), nor do they appear to affect EPSC kinetics (Liu and Cull-Candy, 2002); the latter is consistent with our findings. Therefore the developmental reduction in postsynaptic strength most likely results from fewer AMPARs activated by the release of glutamate from the fusion of a single vesicle. “

The authors correctly identify the relationship between local dendritic resistance and the reduction of driving force, but they assume the same relationship for young SCs as well in their model. This assumption is not supported by recordings, and as there are several publications about the disparity of input impedance for young versus adult cells (Schmidt-Hieber, Bischoffberger 2007).

The input resistance of the dendrite will indeed determine local depolarization and loss of driving force. However, its impact on dendritic integration depends on it precise value, and perhaps the reviewer thought we “assumed” that the input resistance to be the same between immature and adult SCs. This was not the case, and we have since clarified this in the manuscript. We performed three important measurements that support a loss of driving force in immature SCs (for reference, the input resistance for an infinite cable is described by the following equation (Rn= sqrt(RmRi/2)/(2pi*r^(3/2)), where r is the dendrite radius):

1) The input resistance is inversely proportional to the dendritic diameter, which we measured to be only slightly larger in immature SCs (0.47 versus 0.41 μm). This result is described in Figure 2.

2) We measured the membrane time constant, which provides an estimate of the total membrane conductance multiplied by the total capacitance. The values between the two ages were similar, suggesting a slightly larger membrane resistance to compensate the smaller total membrane capacitance of the immature SCs. This was explicitly accounted for when performing the simulations using reconstructed immature and adult SCs (Figure 2 and 7 and 8) by adjusting the specific membrane resistance until the simulated membrane time constant matched experimental values. These values were not clearly mentioned and are now included on line 233 in the Results and 704 in the Methods.

3) We directly examined paired-pulse facilitation of synapses onto immature SC dendrites versus that for somatic synapses. We previously showed in adult SCs that sublinear summation of synaptic responses, due to loss of synaptic current driving force (Tran- Van-Minh et al. 2016), manifests in decreased facilitation for dendritic synapses (Abrahamsson et al. 2012). Figure 8A shows that indeed dendritic facilitation was less than observed in the soma. We have now modified Figure 8 to include the results of the simulations showing that the biophysical model could reproduce this difference in shortterm plasticity (Figure 8B).

Together, we believe these measurements support the presence of similar sublinear summation mechanisms in immature SCs.

2) The authors use extracellular stimulation of parallel fibers. The authors note that due to the orientation of the PF, and the slicing angle, they can restrict the spatial extent of the stimuli. However, this method does not guarantee that the stimulated fibers will all connect to the same dendritic branch. Whether two stimulated synapses connect to the same dendrite or not can heavily influence summation. This is especially a great concern for these cells as the Scholl analysis showed that young and adult SC cells have different amount of distal dendrites. Therefore, if the stimulated axons connect to several different neighboring dendrites instead of the one or two in case of young SC cells, then the model calculations and the conclusions about the summation rules may be erroneous.

We selected isolated dendrites and delivered voltage stimuli using small diameter glass electrodes (~ 1 μm) 10 - 15 V above threshold to stimulate single dendrites. This procedure excites GC axons in brain slices made from adult mice within less than 10 μm from the tip (Figure 2C, Tran-Van-Minh et al. 2016). It produces large dendritic depolarizations that are sufficient to decrease synaptic current driving force (Figure 1, Tran-Van-Minh et al. 2016). When we reproduced the conductance ratio using uncaging of single dendrites, we observed paired-pulse facilitation in the dendrites – suggesting that electrical stimulation activated synapses on common dendritic branches, or at least within close electrotonic distance to cause large dendritic depolarizations (Figure 7, Abrahamsson et al. 2012). Finally, we expect that the decreased branching in immature SCs further ensures that a majority of recorded synapses are contacting a common dendritic segment. We cannot rule out that occasionally some synaptic responses recorded at the soma are from synapses on different dendritic branches, but we do not see how this would alter our results and change our principal conclusions, particularly since this possible error only effects the interpretation of how many synapses are activated in paired-pulse experiments. The majority of the conclusions arise from the stimulation of single vesicle release events, and given the strikingly perpendicular orientation of GC axons, a 10 μm error in synapse location along a dendrite when we stimulated in the outthird would not alter our interpretations of the data.

eLife Assessment

This important work provides mechanistic insights into the development of cardiac arrhythmia and establishes a new experimental use case for optogenetics in studying cardiac electrophysiology. The agreement between computational models and experimental observations provides a convincing level of evidence that wave train-induced pacemaker activity can originate in continuously depolarized tissue, with the limitation that there may be differences between depolarization arising from constant optogenetic stimulation, as opposed to pathophysiological tissue depolarization. Future experiments in vivo and in other tissue preparations would extend the generality of these findings.

Reviewer #1 (Public review):

Summary:

The study by Teplenin and coworkers assesses the combined effects of localized depolarization and excitatory electrical stimulation in myocardial monolayers. They study the electrophysiological behaviour of cultured neonatal rat ventricular cardiomyocytes expressing the light-gated cation channel Cheriff, allowing them to induce local depolarization of varying area and amplitude, the latter titrated by the applied light intensity. In addition, they used computational modeling to screen for critical parameters determining state transitions, and for dissecting the underlying mechanisms. Two stable states, thus bistability, could be induced upon local depolarization and electrical stimulation, one state characterized by a constant membrane voltage and a second spontaneously firing, thus oscillatory state. The resulting 'state' of the monolayer was dependent on the duration and frequency of electrical stimuli, as well as the size of the illuminated area and the applied light intensity determining the degree of depolarization as well as the steepness of the local voltage gradient. In addition to the induction of oscillatory behaviour, they also tested frequency-dependent termination of induced oscillations.

Strengths:

The data from optogenetic experiments and computational modelling provide quantitative insights into the parameter space determining the induction of spontaneous excitation in the monolayer. The most important findings can also be reproduced using a strongly reduced computational model, suggesting that the observed phenomena might be more generally applicable.

Weaknesses:

While the study is thoroughly performed and provides interesting mechanistic insights into scenarios of ventricular arrhythmogenesis in the presence of localized depolarized tissue areas, the translational perspective of the study remains relatively vague. In addition, the chosen theoretical approach and the way the data is presented might make it difficult for the wider community of cardiac researchers to understand the significance of the study.

Comments on Revision:

The provided revisions address some of the raised concerns, but they do not change my general assessment of the paper, including its strengths and weaknesses.

Reviewer #2 (Public review):

In the presented manuscript, Teplenin and colleagues use both electrical pacing and optogenetic stimulation to create a reproducible, controllable source of ectopy in cardiomyocyte monolayers. To accomplish this, they use a careful calibration of electrical pacing characteristics (i.e., frequency, number of pulses) and illumination characteristics (i.e., light intensity, surface area) to show that there exists a "sweet spot" where oscillatory excitations can emerge proximal to the optogenetically depolarized region following electrical pacing cessation, akin to pacemaker cells. Furthermore, the authors demonstrate that a high-frequency electrical wave-train can be used to terminate these oscillatory excitations. The authors observed this oscillatory phenomenon both in vitro (using neonatal rat ventricular cardiomyocyte monolayers) and in silico (using a computational action potential model of the same cell type). These are surprising findings and provide a novel approach for studying triggered activity in cardiac tissue.

The study is extremely thorough and one of the more memorable and grounded applications of cardiac optogenetics in the past decade. One of the benefits of the authors' "two-prong" approach of experimental preps and computational models is that they could probe the number of potential variable combinations much deeper than through in vitro experiments alone. The strong similarities between the real-life and computational findings suggest that these oscillatory excitations are consistent, reproducible, and controllable.

Triggered activity, which can lead to ventricular arrhythmias and cardiac sudden death, has been largely contributed to sub-cellular phenomena, such as early or delayed afterdepolarizations, and thus to date has largely been studied in isolated single cardiomyocytes. However, these findings have been difficult to translate to tissue- and organ-scale experiments, as well-coupled cardiac tissue has notably different electrical properties. This underscores the significance of the study's methodological advances: use of a constant depolarizing current in a subset of (illuminated) cells to reliably result in triggered activity could facilitate the more consistent evaluation of triggered activity at various scales. An experimental prep that is both repeatable and controllable (i.e., both initiated and terminated through the same means) is a boon for further inquiry.

The authors also substantially explored phase space and single cell analyses to document how this "hidden" bi-stable phenomenon can be uncovered during emergent collective tissue behavior. Calibration and testing of different aspects (e.g.: light intensity, illuminated surface area, electrical pulse frequency, electrical pulse count) and other deeper analyses, as illustrated in Figures S3-S8 and Video S1, are significant and commendable.

Given the study is computational, it is surprising that the authors did not replicate their findings using well-validated adult ventricular cardiomyocyte action potential models, such ten Tusscher 2006 or O'Hara 2011. This may have felt out-of-scope, given the nice alignment of rat cardiomyocyte data between in vitro and in silico experiments. However, it would have been helpful peace-of-mind validation, given the significant ionic current differences between neonatal rat and adult ventricular tissue. It is not fully clear whether the pulse trains could have resulted in the same bi-stable oscillatory behavior, given the longer APD of humans relative to rats. The observed phenomenon certainly would be frequency-dependent and would have required tedious calibration for a new cell type, albeit partially mitigated by the relative ease of in silico experiments.

There are likely also mechanistic differences between this optogenetically-tied oscillatory behavior and triggered activity observed in other studies. This is because the constant light-elicited depolarizing current is disrupting the typical resting cardiomyocyte state, thereby altering the balance between depolarizing ionic currents (such as Na+ and Ca2+) and repolarizing ionic currents (such as K+ and Ca2+). The oscillatory excitations appear to later emerge at the border of the illuminated region and non-stimulated surrounding tissue, which is likely an area of high source-sink mismatch. The authors appear to acknowledge differences in this oscillatory behavior and previous sub-cellular triggered activity research in their discussion of ectopic pacemaker activity, which are canonically observed in genetic, pharmacologic, or pathological ionic conditions. Regardless, it is exciting to see new ground being broken in this difficult-to-characterize experimental space, even if the method illustrated here may not necessarily be broadly applicable.

Comments on revisions:

I have read the authors' rebuttal to our earlier comments and do not have any further questions or comments. Thank you for implementing the minor improvements to Figure visualizations and for creating Video S1 to accompany the article.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Teplenin and coworkers assesses the combined effects of localized depolarization and excitatory electrical stimulation in myocardial monolayers. They study the electrophysiological behaviour of cultured neonatal rat ventricular cardiomyocytes expressing the light-gated cation channel Cheriff, allowing them to induce local depolarization of varying area and amplitude, the latter titrated by the applied light intensity. In addition, they used computational modeling to screen for critical parameters determining state transitions and to dissect the underlying mechanisms. Two stable states, thus bistability, could be induced upon local depolarization and electrical stimulation, one state characterized by a constant membrane voltage and a second, spontaneously firing, thus oscillatory state. The resulting 'state' of the monolayer was dependent on the duration and frequency of electrical stimuli, as well as the size of the illuminated area and the applied light intensity, determining the degree of depolarization as well as the steepness of the local voltage gradient. In addition to the induction of oscillatory behaviour, they also tested frequency-dependent termination of induced oscillations.

Strengths:

The data from optogenetic experiments and computational modelling provide quantitative insights into the parameter space determining the induction of spontaneous excitation in the monolayer. The most important findings can also be reproduced using a strongly reduced computational model, suggesting that the observed phenomena might be more generally applicable.

Weaknesses:

While the study is thoroughly performed and provides interesting mechanistic insights into scenarios of ventricular arrhythmogenesis in the presence of localized depolarized tissue areas, the translational perspective of the study remains relatively vague. In addition, the chosen theoretical approach and the way the data are presented might make it difficult for the wider community of cardiac researchers to understand the significance of the study.

Reviewer #2 (Public review):

In the presented manuscript, Teplenin and colleagues use both electrical pacing and optogenetic stimulation to create a reproducible, controllable source of ectopy in cardiomyocyte monolayers. To accomplish this, they use a careful calibration of electrical pacing characteristics (i.e., frequency, number of pulses) and illumination characteristics (i.e., light intensity, surface area) to show that there exists a "sweet spot" where oscillatory excitations can emerge proximal to the optogenetically depolarized region following electrical pacing cessation, akin to pacemaker cells. Furthermore, the authors demonstrate that a high-frequency electrical wave-train can be used to terminate these oscillatory excitations. The authors observed this oscillatory phenomenon both in vitro (using neonatal rat ventricular cardiomyocyte monolayers) and in silico (using a computational action potential model of the same cell type). These are surprising findings and provide a novel approach for studying triggered activity in cardiac tissue.

The study is extremely thorough and one of the more memorable and grounded applications of cardiac optogenetics in the past decade. One of the benefits of the authors' "two-prong" approach of experimental preps and computational models is that they could probe the number of potential variable combinations much deeper than through in vitro experiments alone. The strong similarities between the real-life and computational findings suggest that these oscillatory excitations are consistent, reproducible, and controllable.

Triggered activity, which can lead to ventricular arrhythmias and cardiac sudden death, has been largely attributed to sub-cellular phenomena, such as early or delayed afterdepolarizations, and thus to date has largely been studied in isolated single cardiomyocytes. However, these findings have been difficult to translate to tissue and organ-scale experiments, as well-coupled cardiac tissue has notably different electrical properties. This underscores the significance of the study's methodological advances: the use of a constant depolarizing current in a subset of (illuminated) cells to reliably result in triggered activity could facilitate the more consistent evaluation of triggered activity at various scales. An experimental prep that is both repeatable and controllable (i.e., both initiated and terminated through the same means).

The authors also substantially explored phase space and single-cell analyses to document how this "hidden" bi-stable phenomenon can be uncovered during emergent collective tissue behavior. Calibration and testing of different aspects (e.g., light intensity, illuminated surface area, electrical pulse frequency, electrical pulse count) and other deeper analyses, as illustrated in Appendix 2, Figures 3-8, are significant and commendable.

Given that the study is computational, it is surprising that the authors did not replicate their findings using well-validated adult ventricular cardiomyocyte action potential models, such as ten Tusscher 2006 or O'Hara 2011. This may have felt out of scope, given the nice alignment of rat cardiomyocyte data between in vitro and in silico experiments. However, it would have been helpful peace-of-mind validation, given the significant ionic current differences between neonatal rat and adult ventricular tissue. It is not fully clear whether the pulse trains could have resulted in the same bi-stable oscillatory behavior, given the longer APD of humans relative to rats. The observed phenomenon certainly would be frequency-dependent and would have required tedious calibration for a new cell type, albeit partially mitigated by the relative ease of in silico experiments.

For all its strengths, there are likely significant mechanistic differences between this optogenetically tied oscillatory behavior and triggered activity observed in other studies. This is because the constant light-elicited depolarizing current is disrupting the typical resting cardiomyocyte state, thereby altering the balance between depolarizing ionic currents (such as Na+ and Ca2+) and repolarizing ionic currents (such as K+ and Ca2+). The oscillatory excitations appear to later emerge at the border of the illuminated region and non-stimulated surrounding tissue, which is likely an area of high source-sink mismatch. The authors appear to acknowledge differences in this oscillatory behavior and previous sub-cellular triggered activity research in their discussion of ectopic pacemaker activity, which is canonically expected more so from genetic or pathological conditions. Regardless, it is exciting to see new ground being broken in this difficult-to-characterize experimental space, even if the method illustrated here may not necessarily be broadly applicable.

We thank the reviewers for their thoughtful and constructive feedback, as well as for recognizing the conceptual and technical strengths of our work. We are especially pleased that our integrated use of optogenetics, electrical pacing, and computational modelling was seen as a rigorous and innovative approach to investigating spontaneous excitability in cardiac tissue.

At the core of our study was the decision to focus exclusively on neonatal rat ventricular cardiomyocytes. This ensured a tightly controlled and consistent environment across experimental and computational settings, allowing for direct comparison and deeper mechanistic insight. While extending our findings to adult or human cardiomyocytes would enhance translational relevance, such efforts are complicated by the distinct ionic properties and action potential dynamics of these cells, as also noted by Reviewer #2. For this foundational study, we chose to prioritize depth and clarity over breadth.

Our computational domain was designed to faithfully reflect the experimental system. The strong agreement between both domains is encouraging and supports the robustness of our framework. Although some degree of theoretical abstraction was necessary (thereby sometimes making it a bit harder to read), it reflects the intrinsic complexity of the collective behaviours we aimed to capture such as emergent bi-stability. To make these ideas more accessible, we included simplified illustrations, a reduced model, and extensive supplementary material.

A key insight from our work is the emergence of oscillatory behaviour through interaction of illuminated and non-illuminated regions. Rather than replicating classical sub-cellular triggered activity, this behaviour arises from systems-level dynamics shaped by the imposed depolarizing current and surrounding electrotonic environment. By tuning illumination and local pacing parameters, we could reproducibly induce and suppress these oscillations, thereby providing a controllable platform to study ectopy as a manifestation of spatial heterogeneity and collective dynamics.

Altogether, our aim was to build a clear and versatile model system for investigating how spatial structure and pacing influence the conditions under which bistability becomes apparent in cardiac tissue. We believe this platform lays strong groundwork for future extensions into more physiologically and clinically relevant contexts.

In revising the manuscript, we carefully addressed all points raised by the reviewers. We have also responded to each of their specific comments in detail, which are provided below.

Recommendations for the Authors:

Reviewer #1 (Recommendations for the authors):

Please find my specific comments and suggestions below:

(1) Line 64: When first introduced, the concept of 'emergent bi-stability' may not be clear to the reader.

We concur that the full breadth of the concept of emergent bi-stability may not be immediately clear upon first mention. Nonetheless, its components have been introduced separately: “emergent” was linked to multicellular behaviour in line 63, while “bi-stability” was described in detail in lines 39–56. We therefore believe that readers could form an intuitive understanding of the combined term, which will be further clarified as the manuscript develops. To further ease comprehension of the reader, we have added the following clarification to line 64:

“Within this dynamic system of cardiomyocytes, we investigated emergent bi-stability (a concept that will be explained more thoroughly later on) in cell monolayers under the influence of spatial depolarization patterns.”

(2) Lines 67-80: While the introduction until line 66 is extremely well written, the introduction of both cardiac arrhythmia and cardiac optogenetics could be improved. It is especially surprising that miniSOG is first mentioned as a tool for optogenetic depolarisation of cardiomyocytes, as the authors would probably agree that Channelrhodopsins are by far the most commonly applied tools for optogenetic depolarisation (please also refer to the literature by others in this respect). In addition, miniSOG has side effects other than depolarisation, and thus cannot be the tool of choice when not directly studying the effects of oxidative stress or damage.

The reviewer is absolutely correct in noting that channelrhodopsins are the most commonly applied tools for optogenetic depolarisation. We introduced miniSOG primarily for historical context: the effects of specific depolarization patterns on collective pacemaker activity were first observed with this tool (Teplenin et al., 2018). In that paper, we also reported ultralong action potentials, occurring as a side effect of cumulative miniSOG-induced ROS damage. In the following paragraph (starting at line 81), we emphasize that membrane potential can be controlled much better using channelrhodopsins, which is why we employed them in the present study.

(3) Line 78: I appreciate the concept of 'high curvature', but please always state which parameter(s) you are referring to (membrane voltage in space/time, etc?).

We corrected our statement to include the specification of space curvature of the depolarised region:

“In such a system, it was previously observed that spatiotemporal illumination can give rise to collective behaviour and ectopic waves (Teplenin et al. (2018)) originating from illuminated/depolarised regions (with high spatial curvature).”

(4) Line 79: 'bi-stable state' - not yet properly introduced in this context.

The bi-stability mentioned here refers back to single cell bistability introduced in Teplenin et al. (2018), which we cited again for clarity.

“These waves resulted from the interplay between the diffusion current and the single cell bi-stable state (Teplenin et al. (2018)) that was induced in the illuminated region.”

(5) Line 84-85: 'these ion channels allow the cells to respond' - please describe the channel used; and please correct: the channels respond to light, not the cells. Re-ordering this paragraph may help, because first you introduce channels for depolarization, then you go back to both de- and hyperpolarization. On the same note, which channels can be used for hyperpolarization of cardiomyocytes? I am not aware of any, even WiChR shows depolarizing effects in cardiomyocytes during prolonged activation (Vierock et al. 2022). Please delete: 'through a direct pathway' (Channelrhodopsins a directly light-gated channels, there are no pathways involved).

We realised that the confusion arose from our use of incorrect terminology: we mistakenly wrote hyperpolarisation instead of repolarisation. In addition to channelrhodopsins such as WiChR, other tools can also induce a repolarising effect, including light-activatable chloride pumps (e.g., JAWS). However, to improve clarity, we recognize that repolarisation is not relevant to our manuscript and therefore decided to remove its mention (see below). Regarding the reported depolarising effects of WiChR in Vierock et al. (2022), we speculate that these may arise either from the specific phenotype of the cardiomyocytes used in the study, i.e. human induced pluripotent stem cell-derived atrial myocytes (aCMs), or from the particular ionic conditions applied during patch-clamp recordings (e.g., a bath solution containing 1 mM KCl). Notably, even after prolonged WiChR activation, the aCMs maintained a strongly negative maximum diastolic potential of approximately –55 mV.

“Although effects of illuminating miniSOG with light might lead to formation of depolarised areas, it is difficult to control the process precisely since it depolarises cardiomyocytes indirectly. Therefore, in this manuscript, we used light-sensitive ion channels to obtain more refined control over cardiomyocyte depolarisation. These ion channels allow the cells to respond to specific wavelengths of light, facilitating direct depolarisation (Ördög et al. (2021, 2023)). By inducing cardiomyocyte depolarisation only in the illuminated areas, optogenetics enables precise spatiotemporal control of cardiac excitability, an attribute we exploit in this manuscript (Appendix 2 Figure 1).”

(6) Figure 1: What would be the y-axis of the 'energy-like curves' in B? What exactly did you plot here?

The graphs in Figure 1B are schematic representations intended to clarify the phenomenon for the reader. They do not depict actual data from any simulation or experiment. We clarified this misunderstanding by specifying that Figure 1B is a schematic representation of the effects at play in this paper.

“(B) Schematic representation showing how light intensity influences collective behaviour of excitable systems, transitioning between a stationary state (STA) at low illumination intensities and an oscillatory state (OSC) at high illumination intensities. Bi-stability occurs at intermediate light intensities, where transitions between states are dependent on periodic wave train properties. TR. OSC, transient oscillations.”

To expand slightly beyond the paper: our schematic representation was inspired by a common visualization in dynamical systems used to illustrate bi-stability (for an example, see Fig. 3 in Schleimer, J. H., Hesse, J., Contreras, S. A., & Schreiber, S. (2021). Firing statistics in the bistable regime of neurons with homoclinic spike generation. Physical Review E, 103(1), 012407.). In this framework, the y-axis can indeed be interpreted as an energy landscape, which is related to a probability measure through the Boltzmann distribution: . Here, p denotes the probability of occupying a particular state (STA or OSC). This probability can be estimated from the area (BCL × number of pulses) falling within each state, as shown in Fig. 4C. Since an attractor corresponds to a high-probability state, it naturally appears as a potential well in the landscape.

(7) Lines 92-93: 'this transition resulted for the interaction of an illuminated region with depolarized CM and an external wave train' - please consider rephrasing (it is not the region interacting with depolarized CM; and the external wave train could be explained more clearly).

We rephrased our unclear sentence as follows:

“This transition resulted from the interaction of depolarized cardiomyocytes in an illuminated region with an external wave train not originating from within the illuminated region.”

(8) Figure 2 and elsewhere: When mentioning 'frequency', please state frequency values and not cycle lengths. Please also reconsider your distinction between high and low frequencies; 200 ms (5 Hz) is actually the normal heart rate for neonatal rats (300 bpm).

In the revised version, we have clarified frequency values explicitly and included them alongside period values wherever frequency is mentioned, to avoid any ambiguity. We also emphasize that our use of "high" and "low" frequency is strictly a relative distinction within the context of our data, and not meant to imply a biological interpretation.

(9) Lines 129-131: Why not record optical maps? Voltage dynamics in the transition zone between depolarised and non-depolarised regions might be especially interesting to look at?

We would like to clarify that optical maps were recorded for every experiment, and all experimental traces of cardiac monolayer activity were derived from these maps. We agree with the reviewer that the voltage dynamics in the transition zone are particularly interesting. However, we selected the data representations that, in our view, best highlight the main mechanisms. When we analysed full voltage profiles, they didn’t add extra insights to this main mechanism. As the other reviewer noted, the manuscript already presents a wide range of regimes, so we decided not to introduce further complexity.

(10) Lines 156-157: Why was the model not adapted to match the biophysical properties (e.g., kinetics, ion selectivity, light sensitivity) of Cheriff?

The model was not adapted to the biophysical properties of Cheriff, because this would entail a whole new study involving extensive patch-clamping experiments, fitting, and calibration to model the correct properties of the ion channel. Beyond considerations of time efficiency, incorporating more specific modelling parameters would not change the essence of our findings. While numeric parameter ranges might shift, the core results would remain unchanged. This is a result of our experimental design where we applied constant illumination of long duration (6s or longer), thus making a difference in kinetical properties of an optogenetic tool irrelevant. In addition, we were able to observe qualitatively similar phenomena using many other depolarising optogenetic tools (e.g. ChR2, ReaChR, CatCh and more) in our in-vitro experiments. We ended up with Cheriff as our optotool-of-choice for the practical reasons of good light-sensitivity and a non-overlapping spectrum with our fluorescent dyes.

Therefore, computationally using a more general depolarising ion channel hints at the more general applicability of the observed phenomena, supporting our claim of a universal mechanism  (demonstrated experimentally with CheRiff and computationally with ChR2).

(11) Line 158: 1.7124 mW/mm^2 - While I understand that this is the specific intensity used as input in the model, I am convinced that the model is not as accurate to predict behaviour at this specific intensity (4 digits after the comma), especially given that the model has not been adapted to Cheriff (probably more light sensitive than ChR2). Can this be rephrased?

We did not aim for quantitative correspondence between the computational model and the biological experiments, but rather for qualitative agreement and mechanistic insight (see line 157). Qualitative comparisons are computationally obtained in a whole range of different intensities, as demonstrated in the 3D diagram of Fig. 4C. We wanted to demonstrate that at one fixed light intensity (chosen to be 1.7124 mW/mm^2 for the most clear effect), it was possible for all three states (STA, OSC. TR. OSC.) to coexist depending on the number of pulses and their period. Therefore the specific intensity used in the computational model is correct, and for reproducibility, we have left it unchanged while clarifying that it refers specifically to the in silico model:

“Simulating at a fixed constant illumination of 1.7124 𝑚𝑊∕𝑚𝑚² and a fixed number of 4 pulses, frequency dependency of collective bi-stability was reproduced in Figure 4A.”

(12) Lines 160, 165, and elsewhere: 'Once again, Once more' - please delete or rephrase.

We agree that we could have written these binding words better and reformulated them to:

“Similar to the experimental observations, only intermediate electrical pacing frequencies (500-𝑚𝑠 period) caused transitions from collective stationary behaviour to collective oscillatory behaviour and ectopic pacemaker activity had periods (710 𝑚𝑠) that were different from the stimulation train period (500 𝑚𝑠). Figure 4B shows the accumulation of pulses necessary to invoke a transition from the collective stationary state to the collective oscillatory state at a fixed stimulation period (600 𝑚𝑠). Also in the in silico simulations, ectopic pacemaker activity had periods (750 𝑚𝑠) that were different from the stimulation train period (600 𝑚𝑠). Also for the transient oscillatory state, the simulations show frequency selectivity (Appendix 2 Figure 4B).”

(13) Line 171: 'illumination strength': please refer to 'light intensity'.

We have revised our formulation to now refer specifically to “light intensity”:

“We previously identified three important parameters influencing such transitions: light intensity, number of pulses, and frequency of pulses.”

(14) Lines 187-188: 'the illuminated region settles into this period of sending out pulses' - please rephrase, the meaning is not clear.

We reformulated our sentence to make its content more clear to the reader:

“For the conditions that resulted in stable oscillations, the green vertical lines in the middle and right slices represent the natural pacemaker frequency in the oscillatory state. After the transition from the stationary towards the oscillatory state, oscillatory pulses emerging from the illuminated region gradually dampen and stabilize at this period, corresponding to the natural pacemaker frequency.”

(15) Figure 7: A)- please state in the legend which parameter is plotted on the y-axis (it is included in the main text, but should be provided here as well); C) The numbers provided in brackets are confusing. Why is (4) a high pulse number and (3) a low pulse number? Why not just state the number of pulses and add alpha, beta, gamma, and delta for the panels in brackets? I suggest providing the parameters (e.g., 800 ms cycle length, 2 pulses, etc) for all combinations, but not rate them with low, high, etc. (see also comment above).

We appreciate the reviewer’s comments and have revised the caption for figure 7, which now reads as follows:

“Figure 7. Phase plane projections of pulse-dependent collective state transitions. (A) Phase space trajectories (displayed in the Voltage – x_r plane) of the NRVM computational model show a limit cycle (OSC) that is not lying around a stable fixed point (STA). (B) Parameter space slice showing the relationship between stimulation period and number of pulses for a fixed illumination intensity (1.72 𝑚𝑊 ∕𝑚𝑚2) and size of the illuminated area (67 pixels edge length). Letters correspond to the graphs shown in C. (C) Phase space trajectories for different combinations of stimulus train period and number of pulses (α: 800 ms cycle length + 2 pulses, β: 800 ms cycle length + 4 pulses, γ: 250 ms cycle length + 3 pulses, δ: 250 ms cycle length + 8 pulses). α and δ do not result in a transition from the resting state to ectopic pacemaker activity, as under these circumstances the system moves towards the stationary stable fixed point from outside and inside the stable limit cycle, respectively. However, for β and γ, the stable limit cycle is approached from outside and inside, respectively, and ectopic pacemaker activity is induced.”

(16) Line 258: 'other dimensions by the electrotonic current' - not clear, please rephrase and explain.

We realized that our explanation was somewhat convoluted and have therefore changed the text as follows:

“Rather than producing oscillations, the system returns to the stationary state along dimensions other than those shown in Figure 7C (Voltage and x_r), as evidenced by the phase space trajectory crossing itself. This return is mediated by the electrotonic current.”

(17) Line 263: ‘increased too much’ – please rephrase using scientific terminology.

We rephrased our sentence to:

“However, this is not a Hopf bifurcation, because in that case the system would not return to the stationary state when the number of pulses exceeds a critical threshold.”

(18) Line 275: 'stronger diffusion/electrotonic influence from the non-illuminated region' - not sure diffusion is the correct term here. Please explain by taking into account the membrane potential. Please make sure to use proper terminology. The same applies to lines 281-282.

We appreciate this comment, which prompted us to revisit on our text. We realised that some sections could be worded more clearly, and we also identified an error in the legend of Supplementary Figure 7. The corresponding corrections are provided below:

“However, repolarisation reserve does have an influence, prolonging the transition when it is reduced (Appendix 2 Figure 7). This effect can be observed either by moving further from the boundary of the illuminated region, where the electrotonic influence from the non-illuminated region is weaker, or by introducing ionic changes, such as a reduction in I_Ks and/or I_to. For example, because the electrotonic influence is weaker in the center of the illuminated region, the voltage there is not pulled down toward the resting membrane potential as quickly as in cells at the border of the illuminated zone.”

“To add a multicellular component to our single cell model we introduced a current that replicates the effect of cell coupling and its associated electrotonic influence.”

“Figure 7. The effect of ionic changes on the termination of pacemaker activity. The mechanism that moves the oscillating illuminated tissue back to the stationary state after high frequency pacing is dependent on the ionic properties of the tissue, i.e. lower repolarisation reserves (20% 𝐼_𝐾𝑠 + 50% 𝐼_𝑡𝑜) are associated with longer transition times.”

(19) Line 289: -58 mV (to be corrected), -20 mV, and +50 mV - please justify the selection of parameters chosen. This also applies elsewhere- the selection of parameters seems quite arbitrary, please make sure the selection process is more transparent to the reader.

Our choice of parameters was guided by the dynamical properties of the illuminated cells as well as by illustrative purposes. The value of –58 mV corresponds to the stimulation threshold of the model. The values of 50 mV and –20 mV match those used for single-cell stimulation (Figure 8C2, right panel), producing excitable and bistable dynamics, respectively. We refer to this point in line 288 with the phrase “building on this result.” To maintain conciseness, we did not elaborate on the underlying reasoning within the manuscript and instead reported only the results.

We also corrected the previously missed minus sign: -58 mV.

(20) Figure 8 and corresponding text: I don't understand what stimulation with a voltage means. Is this an externally applied electric field? Or did you inject a current necessary to change the membrane voltage by this value? Please explain.

Stimulation with a specific voltage is a standard computational technique and can be likened to performing a voltage-clamp experiment on each individual cell. In this approach, the voltage of every cell in the tissue is briefly forced to a defined value.

(21) Figure 8C- panel 2: Traces at -20 mV and + 50 mV are identical. Is this correct? Please explain.

Yes, that is correct. The cell responds similarly to a voltage stimulus of -20 mV or one of 50 mV, because both values are well above the excitation threshold of a cardiomyocyte.

(22) Line 344 and elsewhere: 'diffusion current' - This is probably not the correct terminology for gap-junction mediated currents. Please rephrase.

A diffusion current is a mathematical formulation for a gap junction mediated current here, so , depending on the background of the reader, one of the terms might be used focusing on different aspects of the results. In a mathematical modelling context one often refers to a diffusion current because cardiomyocytes monolayers and tissues can be modelled using a reaction-diffusion equation. From the context of fine-grain biological and biophysical details, one uses the term gap-junction mediated current. Our choice is motivated by the main target audience we have in mind, namely interdisciplinary researchers with a core background in the mathematics/physics/computer science fields.

However, to not exclude our secondary target audience of biological and medical readers we now clarified the terminology, drawing the parallel between the different fields of study at line 79:

“These waves resulted from the interplay between the diffusion current (also known in biology/biophysics as the gap junction mediated current) and the bi-stable state that was induced in the illuminated region.”

(23) Lines 357-58: 'Such ectopic sources are typically initiated by high frequency pacing' - While this might be true during clinical testing, how would you explain this when not externally imposed? What could be biological high-frequency triggers?

Biological high-frequency triggers could include sudden increases in heart rates, such as those induced by physical activity or emotional stress. Another possibility is the occurrence of paroxysmal atrial or ventricular fibrillation, which could then give rise to an ectopic source.

(24) Lines 419-420: 'large ionic cell currents and small repolarising coupling currents'. Are coupling currents actually small in comparison to cellular currents? Can you provide relative numbers (~ratio)?

Coupling currents are indeed small compared to cellular currents. This can be inferred from the I-V curve shown in Figure 8C1, which dips below 0 and creates bi-stability only because of the small coupling current. If the coupling current were larger, the system would revert to a monostable regime. To make this more concrete, we have now provided the exact value of the coupling current used in Figure 8C1.

“Otherwise, if the hills and dips of the N-shaped steady-state IV curve were large (Figure 8C-1), they would have similar magnitudes as the large currents of fast ion channels, preventing the subtle interaction between these strong ionic cell currents and the small repolarising coupling currents (-0.103649 ≈ 0.1 pA).”

(25) Line 426: Please explain how ‘voltage shocks’ were modelled.

We would like to refer the reviewer to our response to comment (20) regarding how we model voltage shocks. In the context of line 426, a typical voltage shock corresponds to a tissue-wide stimulus of 50 mV. Independent of our computational model, line 426 also cites other publications showing that, in clinical settings, high-voltage shocks are unable to terminate ectopic sustained activity, consistent with our findings.

(26) Lines 429 ff: 0.2pA/pF would correspond to 20 pA for a small cardiomyocyte of 100 pF, this current should be measurable using patch-clamp recordings.

In trying to be succinct, we may have caused some confusion. The difference between the dips (≈-0.07 pA/pF) and hills (_≈_0.11 pA/pF) is approximately 0.18 pA/pF. For a small cardiomyocyte, this corresponds to deviations from zero of roughly ±10 pA. Considering that typical RMS noise levels in whole-cell patch-clamp recordings range from 2-10 pA , it is understandable that detecting these peaks and dips in an I-V curve (average current after holding a voltage for an extended period)  is difficult. Achieving statistical significance would therefore require patching a large number of cells.

Given the already extensive scope of our manuscript in terms of techniques and concepts, we decided not to pursue these additional patch-clamp experiments.

Reviewer #2 (Recommendations for the authors):

Given the deluge of conditions to consider, there are several areas of improvement possible in communicating the authors' findings. I have the following suggestions to improve the manuscript.

(1) Please change "pulse train" straight pink bar OR add stimulation marks (such as "*", or individual pulse icons) to provide better visual clarity that the applied stimuli are "short ON, long OFF" electrical pulses. I had significant initial difficulty understanding what the pulse bars represented in Figures 2, 3, 4A-B, etc. This may be partially because stimuli here could be either light (either continuous or pulsed) or electrical (likely pulsed only). To me, a solid & unbroken line intuitively denotes a continuous stimulation. I understand now that the pink bar represents the entire pulse-train duration, but I think readers would be better served with an improvement to this indicator in some fashion. For instance, the "phases" were much clearer in Figures 7C and 8D because of how colour was used on the Vm(t) traces. (How you implement this is up to you, though!)

We have addressed the reviewer’s concern and updated the figures by marking each external pulse with a small vertical line (see below).

(2) Please label the electrical stimulation location (akin to the labelled stimulation marker in circle 2 state in Figure 1A) in at least Figures 2 and 4A, and at most throughout the manuscript. It is unclear which "edge" or "pixel" the pulse-train is originating from, although I've assumed it's the left edge of the 2D tissue (both in vitro and silico). This would help readers compare the relative timing of dark blue vs. orange optical signal tracings and to understand how the activation wavefront transverses the tissue.

We indicated the pacing electrode in the optical voltage recordings with a grey asterisk. For the in silico simulations, the electrode was assumed to be far away, and the excitation was modelled as a parallel wave originating from the top boundary, indicated with a grey zone.

(3) Given the prevalence of computational experiments in this study, I suggest considering making a straightforward video demonstrating basic examples of STA, OSC, and TR.OSC states. I believe that a video visualizing these states would be visually clarifying to and greatly appreciated by readers. Appendix 2 Figure 3 would be the no-motion visualization of the examples I'm thinking of (i.e., a corresponding stitched video could be generated for this). However, this video-generation comment is a suggestion and not a request.

We have included a video showing all relevant states, which is now part of the Supplementary Material.

(4) Please fix several typos that I found in the manuscript:

(4A) Line 279: a comma is needed after i.e. when used in: "peculiar, i.e. a standard". However, this is possibly stylistic (discard suggestion if you are consistent in the manuscript).

(4B) Line 382: extra period before "(Figure 3C)".

(4C) Line 501: two periods at end of sentence "scientific purposes.." .

We would like to thank the reviewer for pointing out these typos. We have corrected them and conducted an additional check throughout the manuscript for minor errors.

eLife Assessment

The authors investigate arrestin2-mediated CCR5 endocytosis in the context of clathrin and AP2 contributions. Using an extensive set of NMR experiments, and supported by microscopy and other biophysical assays, the authors provide compelling data on the roles of AP2 and clathrin in CCR5 endocytosis. This important work will appeal to an audience beyond those studying chemokine receptors, including those studying GPCR regulation and trafficking. The distinct role of AP2 and not clathrin will be of particular interest to those studying GPCR internalization mechanisms.

Reviewer #1 (Public review):

Petrovic et al. investigate CCR5 endocytosis via arrestin2, with a particular focus on clathrin and AP2 contributions. The study is thorough and methodologically diverse. The NMR titration data clearly demonstrate chemical shift changes at the canonical clathrin-binding site (LIELD), present in both the 2S and 2L arrestin splice variants. To assess the effect of arrestin activation on clathrin binding, the authors compare: truncated arrestin (1-393), full-length arrestin, and 1-393 incubated with CCR5 phosphopeptides. All three bind clathrin comparably, whereas controls show no binding. These findings are consistent with prior crystal structures showing peptide-like binding of the LIELD motif, with disordered flanking regions. The manuscript also evaluates a non-canonical clathrin binding site specific to the 2L splice variant. Though this region has been shown to enhance beta2-adrenergic receptor binding, it appears not to affect CCR5 internalization.

Similar analyses applied to AP2 show a different result. AP2 binding is activation-dependent and influenced by the presence and level of phosphorylation of CCR5-derived phosphopeptides. These findings are reinforced by cellular internalization assays.

In sum, the results highlight splice-variant-dependent effects and phosphorylation-sensitive arrestin-partner interactions. The data argue against a (rapidly disappearing) one-size-fits-all model for GPCR-arrestin signaling and instead support a nuanced, receptor-specific view, with one example summarized effectively in the mechanistic figure.

Weaknesses:

Figure 1 shows regions alphaFold model that are intrinsically disordered without making it clear that this is not an expected stable position. The authors NMR titration data are n=1. Many figure panels require that readers pinch and zoom to see the data.

Reviewer #2 (Public review):

Summary:

Based on extensive live cell assays, SEC, and NMR studies of reconstituted complexes, these authors explore the roles of clathrin and the AP2 protein in facilitating clathrin mediated endocytosis via activated arrestin-2. NMR, SEC, proteolysis, and live cell tracking confirm a strong interaction between AP2 and activated arrestin using a phosphorylated C-terminus of CCR5. At the same time a weak interaction between clathrin and arrestin-2 is observed, irrespective of activation.

These results contrast with previous observations of class A GPCRs and the more direct participation by clathrin. The results are discussed in terms of the importance of short and long phosphorylated bar codes in class A and class B endocytosis.

Strengths:

The 15N,1H and 13C,methyl TROSY NMR and assignments represent a monumental amount of work on arrestin-2, clathrin, and AP2. Weak NMR interactions between arrestin-2 and clathrin are observed irrespective of activation of arrestin. A second interface, proposed by crystallography, was suggested to be a possible crystal artifact. NMR establishes realistic information on the clathrin and AP2 affinities to activated arrestin with both kD and description of the interfaces.

Weaknesses:

This reviewer has identified only minor weaknesses with the study.

(1) I don't observe two overlapping spectra of Arrestin2 (1-393) +/- CLTC NTD in Supp Figure 1

(2) Arrestin-2 1-418 resonances all but disappear with CCR5pp6 addition. Are they recovered with Ap2Beta2 addition and is this what is shown in Supp Fig 2D

(3) I don't understand how methyl TROSY spectra of arrestin2 with phosphopeptide could look so broadened unless there are sample stability problems?

(4) At one point the authors added excess fully phosphorylated CCR5 phosphopeptide (CCR5pp6). Does the phosphopeptide rescue resolution of arrestin2 (NH or methyl) to the point where interaction dynamics with clathrin (CLTC NTD) are now more evident on the arrestin2 surface?

(5) Once phosphopeptide activates arrestin-2 and AP2 binds can phosphopeptide be exchanged off? In this case, would it be possible for the activated arrestin-2 AP2 complex to re-engage a new (phosphorylated) receptor?

(6) I'd be tempted to move the discussion of class A and class B GPCRs and their presumed differences to the intro and then motivate the paper with specific questions.

(7) Did the authors ever try SEC measurements of arrestin-2 + AP2beta2+CCR5pp6 with and without PIP2, and with and without clathrin (CLTC NTD? The question becomes what the active complex is and how PIP2 modulates this cascade of complexation events in class B receptors.

Reviewer #3 (Public review):

Summary:

Overall, this is a well-done study, and the conclusions are largely supported by the data, which will be of interest to the field.

Strengths:

Strengths of this study include experiments with solution NMR that can resolve high-resolution interactions of the highly flexible C-terminal tail of arr2 with clathrin and AP2. Although mainly confirmatory in defining the arr2 CBL 376LIELD380 as the clathrin binding site, the use of the NMR is of high interest (Fig. 1). The 15N-labeled CLTC-NTD experiment with arr2 titrations reveals a span from 39-108 that mediates an arr2 interaction, which corroborates previous crystal data, but does not reveal a second area in CLTC-NTD that in previous crystal structures was observed to interact with arr2.

SEC and NMR data suggest that full-length arr2 (1-418) binding with 2-adaptin subunit of AP2 is enhanced in the presence of CCR5 phospho-peptides (Fig. 3). The pp6 peptide shows the highest degree of arr2 activation, and 2-adaptin binding, compared to less phosphorylated peptide or not phosphorylated at all. It is interesting that the arr2 interaction with CLTC NTD and pp6 cannot be detected using the SEC approach, further suggesting that clathrin binding is not dependent on arrestin activation. Overall, the data suggest that receptor activation promotes arrestin binding to AP2, not clathrin, suggesting the AP2 interaction is necessary for CCR5 endocytosis.

To validate the solid biophysical data, the authors pursue validation experiments in a HeLa cell model by confocal microscopy. This requires transient transfection of tagged receptor (CCR5-Flag) and arr2 (arr2-YFP). CCR5 displays a "class B"-like behavior in that arr2 is rapidly recruited to the receptor at the plasma membrane upon agonist activation, which forms a stable complex that internalizes onto endosomes (Fig. 4). The data suggest that complex internalization is dependent on AP2 binding not clathrin (Fig. 5).

The addition of the antagonist experiment/data adds rigor to the study.

Overall, this is a solid study that will be of interest to the field.

Author response:

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

Reviewer #1 (Public review): 

Petrovic et al. investigate CCR5 endocytosis via arrestin2, with a particular focus on clathrin and AP2 contributions. The study is thorough and methodologically diverse. The NMR titration data are particularly compelling, clearly demonstrating chemical shift changes at the canonical clathrin-binding site (LIELD), present in both the 2S and 2L arrestin splice variants. 

To assess the effect of arrestin activation on clathrin binding, the authors compare: truncated arrestin (1-393), full-length arrestin, and 1-393 incubated with CCR5 phosphopeptides. All three bind clathrin comparably, whereas controls show no binding. These findings are consistent with prior crystal structures showing peptide-like binding of the LIELD motif, with disordered flanking regions. The manuscript also evaluates a non-canonical clathrin binding site specific to the 2L splice variant. Though this region has been shown to enhance beta2-adrenergic receptor binding, it appears not to affect CCR5 internalization. 

Similar analyses applied to AP2 show a different result. AP2 binding is activation-dependent and influenced by the presence and level of phosphorylation of CCR5-derived phosphopeptides. These findings are reinforced by cellular internalization assays. 

In sum, the results highlight splice-variant-dependent effects and phosphorylation-sensitive arrestin-partner interactions. The data argue against a (rapidly disappearing) one-size-fitsall model for GPCR-arrestin signaling and instead support a nuanced, receptor-specific view, with one example summarized effectively in the mechanistic figure. 

We thank the referee for this positive assessment of our manuscript. Indeed, by stepping away from the common receptor models for understanding internalization (b2AR and V2R), we revealed the phosphorylation level of the receptor as a key factor in driving the sequestration of the receptor from the plasma membrane. We hope that the proposed mechanistic model will aid further studies to obtain an even more detailed understanding of forces driving receptor internalization.

Reviewer #2 (Public review): 

Summary: 

Based on extensive live cell assays, SEC, and NMR studies of reconstituted complexes, these authors explore the roles of clathrin and the AP2 protein in facilitating clathrin-mediated endocytosis via activated arrestin-2. NMR, SEC, proteolysis, and live cell tracking confirm a strong interaction between AP2 and activated arrestin using a phosphorylated C-terminus of CCR5. At the same time, a weak interaction between clathrin and arrestin-2 is observed, irrespective of activation. 

These results contrast with previous observations of class A GPCRs and the more direct participation by clathrin. The results are discussed in terms of the importance of short and long phosphorylated bar codes in class A and class B endocytosis. 

Strengths: 

The 15N,1H, and 13C, methyl TROSY NMR and assignments represent a monumental amount of work on arrestin-2, clathrin, and AP2. Weak NMR interactions between arrestin-2 and clathrin are observed irrespective of the activation of arrestin. A second interface, proposed by crystallography, was suggested to be a possible crystal artifact. NMR establishes realistic information on the clathrin and AP2 affinities to activated arrestin, with both kD and description of the interfaces. 

We sincerely thank the referee for this encouraging evaluation of our work and appreciate the recognition of the NMR efforts and insights into the arrestin–clathrin–AP2 interactions.

Weaknesses: 

This reviewer has identified only minor weaknesses with the study.

(1) Arrestin-2 1-418 resonances all but disappear with CCR5pp6 addition. Are they recovered with Ap2Beta2 addition, and is this what is shown in Supplementary Figure 2D? 

We believe the reviewer is referring to Figure 3 - figure supplement 1. In this figure, the panels E and F show resonances of arrestin2^1-418 (apo state shown with black outline) disappear upon the addition of CCR5pp6 (arrestin2^1-418•CCR5pp6 complex spectrum in red). The panels C and D show resonances of arrestin2^1-418 (apo state shown with black outline), which remain unchanged upon addition of AP2b2^701-937 (orange), indicating no complex formation. We also recorded a spectrum of the arrestin2^1-418 •CCR5pp6 complex under addition of AP2b2 ^701-937(not shown), but the arrestin2 resonances in the arrestin2¹⁴¹⁸ •CCR5pp6 complex were already too broad for further analysis. This had been already explained in the text.

“In agreement with the AP2b2 NMR observations, no interaction was observed in the arrestin2 methyl and backbone NMR spectra upon addition of AP2b2 in the absence of phosphopeptide (Figure 3-figure supplement 1C, D). However, the significant line broadening of the arrestin2 resonances upon phosphopeptide addition (Figure 3-figure supplement 1E, F) precluded a meaningful assessment of the effect of the AP2b2 addition on arrestin2 in the presence of phosphopeptide””.

(2) I don't understand how methyl TROSY spectra of arrestin2 with phosphopeptide could look so broadened unless there are sample stability problems. 

We thank the referee for this comment. We would like to clarify that in general a broadened spectrum beyond what is expected from the rotational correlation time does not necessarily correlate with sample stability problems. It is rather evidence of conformational intermediate exchange on the micro- to millisecond time scale.

The displayed ¹H-¹⁵ N spectra of apo arrestin2 already suffer from line broadening due to such intrinsic mobility of the protein. These spectra were recorded with acquisition times of 50 ms (¹⁵N) and 55 ms (¹H) and resolution-enhanced by a 60˚-shifted sine-bell filter for ¹⁵N and a 60˚-shifted squared sine-bell filter for ¹H, respectively, which leads to the observed resolution with still reasonable sensitivity. The ¹H-¹⁵ resonances in Fig. 1b (arrestin2^1-393) look particularly narrow. However, this region contains a large number of flexible residues. The full spectrum, e.g. Figure 1-figure supplement 2, shows the entire situation with a clear variation of linewidths and intensities. The linewidth variation becomes stronger when omitting the resolution enhancement filters.

The addition of the CCR5pp6 phosphopeptide does not change protein stability, which we assessed by measuring the melting temperature of arrestin2^1-418 and arrestin2^1-418 •CCR5pp6 complex (Tm = 57°C in both cases). We believe that the explanation for the increased broadening of the arrestin2 resonances is that addition of the CCR5pp6, possibly due to the release of the arrestin2 strand b20, amplifies the mentioned intermediate timescale protein dynamics. This results in the disappearance of arrestin2 resonances. 

We have now included the assessment of arrestin2^1-418 and arrestin2^1-418 •CCR5pp6 stability in the manuscript:

“The observed line broadening of arrestin2 in the presence of phosphopeptide must be a result of increased protein motions and is not caused by a decrease in protein stability, since the melting temperature of arrestin2 in the absence and presence of phosphopeptide are identical (56.9 ± 0.1 °C)”.

(3) At one point, the authors added an excess fully phosphorylated CCR5 phosphopeptide (CCR5pp6). Does the phosphopeptide rescue resolution of arrestin2 (NH or methyl) to the point where interaction dynamics with clathrin (CLTC NTD) are now more evident on the arrestin2 surface? 

Unfortunately, when we titrate arrestin2 with CCR5pp6 (please see Isaikina & Petrovic et. al, Mol. Cell, 2023 for more details), the arrestin2 resonances undergo fast-to-intermediate exchange upon binding. In the presence of phosphopeptide excess, very few resonances remain, the majority of which are in the disordered region, including resonances from the clathrin-binding loop. Due to the peak overlap, we could not unambiguously assign arrestin2 resonances in the bound state, which precluded our assessment of the arrestin2-clathrin interaction in the presence of phosphopeptide. We have made this now clearer in the paragraph ‘The arrestin2-clathrin interaction is independent of arrestin2 activation’

“Due to significant line broadening and peak overlap of the arrestin2 resonances upon phosphopeptide addition, the influence of arrestin activation on the clathrin interaction could not be detected on either backbone or methyl resonances”.

(4) Once phosphopeptide activates arrestin-2 and AP2 binds, can phosphopeptide be exchanged off? In this case, would it be possible for the activated arrestin-2 AP2 complex to re-engage a new (phosphorylated) receptor?

This would be an interesting mechanism. In principle, this should be possible as long as the other (phosphorylated) receptor outcompetes the initial phosphopeptide with higher affinity towards the binding site. However, we do not have experiments to assess this process directly. Therefore, we rather wish not to further speculate.

(5) Did the authors ever try SEC measurements of arrestin-2 + AP2beta2+CCR5pp6 with and without PIP2, and with and without clathrin (CLTC NTD? The question becomes what the active complex is and how PIP2 modulates this cascade of complexation events in class B receptors. 

We thank the referee for this question. Indeed, we tested whether PIP2 can stabilize the arrestin2•CCR5pp6•AP2 complex by SEC experiments. Unfortunately, the addition of PIP2 increased the formation of arrestin2 dimers and higher oligomers, presumably due to the presence of additional charges. The resolution of SEC experiments was not sufficient to distinguish arrestin2 in oligomeric form or in arrestin2•CCR5pp6•AP2 complex. We now mention this in the text: 

“We also attempted to stabilize the arrestin2-AP2b2-phosphopetide complex through the addition of PIP2, which can stabilize arrestin complexes with the receptor (Janetzko et al., 2022). The addition of PIP2 increased the formation of arrestin2 dimers and higher oligomers, presumably due to the presence of additional charges. Unfortunately, the resolution of the SEC experiments was not sufficient to separate the arrestin2 oligomers from complexes with AP2b2”.

Reviewer #3 (Public review): 

Summary: 

Overall, this is a well-done study, and the conclusions are largely supported by the data, which will be of interest to the field. 

Strengths: 

(1) The strengths of this study include experiments with solution NMR that can resolve high-resolution interactions of the highly flexible C-terminal tail of arr2 with clathrin and AP2. Although mainly confirmatory in defining the arr2 CBL 376LIELD380 as the clathrin binding site, the use of the NMR is of high interest (Figure 1). The 15N-labeled CLTC-NTD experiment with arr2 titrations reveals a span from 39-108 that mediates an arr2 interaction, which corroborates previous crystal data, but does not reveal a second area in CLTC-NTD that in previous crystal structures was observed to interact with arr2.

(2) SEC and NMR data suggest that full-length arr2 (1-418) binding with the 2-adaptin subunit of AP2 is enhanced in the presence of CCR5 phospho-peptides (Figure 3). The pp6 peptide shows the highest degree of arr2 activation and 2-adaptin binding, compared to less phosphorylated peptides or not phosphorylated at all. It is interesting that the arr2 interaction with CLTC NTD and pp6 cannot be detected using the SEC approach, further suggesting that clathrin binding is not dependent on arrestin activation. Overall, the data suggest that receptor activation promotes arrestin binding to AP2, not clathrin, suggesting the AP2 interaction is necessary for CCR5 endocytosis. 

(3) To validate the solid biophysical data, the authors pursue validation experiments in a HeLa cell model by confocal microscopy. This requires transient transfection of tagged receptor (CCR5-Flag) and arr2 (arr2-YFP). CCR5 displays a "class B"-like behavior in that arr2 is rapidly recruited to the receptor at the plasma membrane upon agonist activation, which forms a stable complex that internalizes into endosomes (Figure 4). The data suggest that complex internalization is dependent on AP2 binding, not clathrin (Figure 5). 

We thank the referee for the careful and encouraging evaluation of our work. We appreciate the recognition of the solidity of our data and the support for our conclusions regarding the distinct roles of AP2 and clathrin in arrestin-mediated receptor internalization.

Weaknesses:

The interaction of truncated arr2 (1-393) was not impacted by CCR5 phospho-peptide pp6, suggesting the interaction with clathrin is not dependent on arrestin activation (Figure 2). This raises some questions.

We thank the referee for raising this concern, as we were also surprised by the discovery that the interaction does not depend on arrestin activation. However, the NMR data clearly show at atomic resolution that arrestin activation does not influence the interaction with clathrin in vitro. Evolutionary, the arrestin-clathrin interaction appears not to be conserved as the visual arrestin completely lacks a clathrin-binding motif. For that reason, we believe that the weak arrestin-clathrin interaction provides more of a supportive role during the internalization rather than the regulatory interaction with AP2, which requires and quantitatively depends on the arrestin2 activation. We have reflected on this in the Discussion:

“Although the generalization of this mechanism from CCR5 to other arr-class B receptors has to be explored further, it is indirectly corroborated in the visual rhodopsin-arrestin1 system. The arr-class B receptor rhodopsin (Isaikina et al., 2023) also undergoes CME (Moaven et al., 2013) with arrestin1 harboring the conserved AP2 binding motif, but missing the clathrinbinding motif (Figure 1-figure supplement 1A)”.

Overall, the data are solid, but for added rigor, can these experiments be repeated without tagged receptor and/or arr2? My concern stems from the fact that the stability of the interaction between arr2 and the receptor may be related to the position of the tags.

We thank the referee for this suggestion, which refers to the cellular experiments; the biophysical experiments were carried out without tags. To eliminate the possibility of tags contributing to receptor-arrestin2 binding in the cellular experiments, we also performed the experiments in the presence of CCR5 antagonist [5P12]CCL5 (Figure 4). These data show that in the case of inactive CCR5, arrestin2 is not recruited to CCR5, nor does it form internalization complexes, which would be the case if the tags were increasing the receptorarrestin interaction. In contrast, if the tags were decreasing the interaction, we would not expect such a strong internalization. As indicated below, we have also attempted to perform our cellular experiments using an N-terminally SNAP-tagged CCR5. Unfortunately, this construct did not express in HeLa cells indicating that SNAP-CCR5 was either toxic or degraded.

Reviewing Editor Comments: 

Overall, the reviewers did not suggest much by way of additional experiments. They do suggest several aspects of the manuscript that would benefit from further clarification. 

Reviewer #1 (Recommendations for the authors): 

(1) The distinction between arrestin 2S and arrestin 2L as relates to the canonical and non-canonical clathrin binding sites would benefit from clarification, particularly because the second binding site depends on the splice variant. This is something that some readers may not be familiar with (particularly young ones that are hopefully part of the intended readership).

We thank the referee for this suggestion. We would like to emphasize that in our work, only the long arrestin2 splice variant was used, which contains both binding sites. We have now introduced the splice variants and their relation to the clathrin binding sites in the text. 

In section ‘Localizing and quantifying the arrestin2-clathrin interaction by NMR spectroscopy’:

“Clathrin and arrestin interact in their basal state (Goodman et al., 1996), and a structure of a complex between arrestin2 and the clathrin heavy chain N-terminal domain (residues 1-363, named clathrin-N in the following) has been solved by X-ray crystallography (PDB:3GD1) in the absence of an arrestin2-activating phosphopeptide (Kang et al., 2009). This structure (Figure 1-figure supplement 1B) suggests a 2:1 binding model between arrestin2 and clathrinN. The first interaction (site I) is observed between the ³⁷⁶LIELD³⁸⁰ clathrin-binding motif of the arrestin2 CBL and the edge of the first two β-sheet blades of clathrin-N, whereas the second interaction (site II) occurs between arrestin2 residues ³³⁴LLGDLA³³⁹ and the 4th and 5th blade of clathrin-N. The latter arrestin interaction site is not present in the arrestin2 splice variant arrestin2S (for short) where an 8-amino acid insert (residues 334-341) between β-strands 18 and 19 is removed (Kang et al., 2009)”.

Section ‘The arrestin2-clathrin interaction is independent of arrestin2 activation’

“Figure 2A (left) shows the intensity changes (full spectra in Figure 2-figure supplement 1A) of the clathrin-N ¹H-¹⁵N TROSY resonances [assignments transferred from BMRB, ID:25403 (Zhuo et al., 2015)] upon addition of a one-molar equivalent of arrestin2^1-393. A significant intensity reduction due to line broadening is detected for clathrin-N residues 39-40, 48-50, 62-72, 83-90, 101-106, and 108. These residues form a clearly defined binding region at the edges of blade 1 and blade 2 of clathrin-N (Figure 2A, right), which corresponds to interaction site I in the 3GD1 crystal structure, involving the conserved arrestin2 ³⁷⁶LIELD³⁸⁰ motif. However, no significant signal attenuation was observed for clathrin-N residues in blade 4 and blade 5, which would correspond to the crystal interaction site II with arrestin2 residues ³³⁴LLGDLA³³⁹ that are absent in the arrestin2S splice variant. Thus only one arrestin2 binding site in clathrin-N is detected in solution, and site II of the crystal structure may be a result of crystal packing”.

(2) Acronym density is high throughout. While many are standard in the clathrin literature, this could hinder accessibility for readers with a GPCR or arrestin focus.

We agree with the referee. The acronyms were hard to avoid. The most non-obvious acronym seems ‘CLTC-NTD’ for the N-terminal domain of the clathrin heavy chain, which uses the non-obvious, but common gene name CLTC for the clathrin heavy chain. We have now replaced ‘CLTC-NTD’ by ‘clathrin-N’ and hope that this makes the text easier to follow.

(3) The NMR section, while impressive in scope, had writing that was more difficult to follow than the rest. I am curious what percentage of resonance could be assigned. 

We apologize if the NMR sections of this manuscript were unclear. We attempted to provide a very detailed description of the experimental setup and the spectral results. Being experienced NMR spectroscopists, we have tried very hard to obtain good 3D triple resonance spectra for assignments, but their sensitivity is very low. We believe that this is due to the microsecond dynamics present in the system, which makes the heteronuclear transfers inefficient. So far, we have been able to assign ~30% of the visible arrestin2 resonances. We are still validating the assignments and are working on the analysis and an explanation for this arrestin2 behavior. Therefore, at this point, we want to refrain from stronger statements besides that considerable intrinsic microsecond dynamics is impeding the assignment process.

(4) It may be worth noting in the main text that truncated arrestins have slightly higher basal activation. I was curious why the truncated arrestin was not chosen for the AP2 NMR titrations. Presumably, an effect would be more likely to be seen.

While some truncated arrestin2 variants (comprising residues 1-382 or 1-360) indeed show higher basal activity than the full-length arrestin2, they typically completely lack the b20 strand (residues 386-390), which is crucial for the formation of a parallel b-sheet with strand b1, and whose release governs arrestin activation. Our truncated arrestin2 construct comprises residues 1-393 and contains strand b20. In our experience, no significant difference in basal activity, as assessed by Fab30 binding, was detected for arrestin2^1-393 and arrestin2^1-418 (Author response image 1).

Author response image 1.

SEC profiles showing arrestin2^1–393 (left) and arrestin2^1-418 (right) activation by the CCR5pp6 phosphopeptide as assayed by Fab30 binding. The active ternary arrestin2-phosphopeptide-Fab30 complex elutes at a lower volume than the inactive apo arrestin2 or the binary arrestin2-phosphopeptide complex. Both arrestin2 constructs are activated by the phosphopeptide to a similar level as assessed by the integrated SEC volumes.

We want to emphasize that we used full-length arrestin2^1-418 in order to assess the AP2 interaction, as the crystal structure of arrestin2 peptide-AP2 (PDB:2IV8) shows residues past the residue 393 involved in binding.

PDB codes are currently not accompanied by corresponding literature citations throughout. Please add these. 

Thank you for this suggestion. In the manuscript, we were careful to provide the full literature citation the first time each PDB code is mentioned. To avoid redundancy and maintain clarity, we rather do not want to repeat the citations with every subsequent mentioning of the PDB code.

(5) The AlphaFold model could benefit from a more transparent discussion of prediction confidence and caveats. The younger crowd (part of the presumed intended readership) tends to be more certain that computational output is 'true'. Figure 1A shows long loops that are likely regions of low confidence in the prediction. Displaying expected disordered regions as transparent or color-coded would help highlight these as flexible rather than stable, especially for that same younger readership. 

We need to explain that the AlphaFold model of arrestin2 was only used to visualize the clathrin-binding loop and the 344-loop of the arrestin2 C-domain, which are not detected in the available apo bovine (PDB:1G4M) and apo human (PDB:8AS4) arrestin2 crystal structures. However, the AlphaFold model of arrestin2 is basically identical to the crystal structures in the regions that are visible in the crystal structures. We have clarified this now in the caption to Figure 1.

“The model was used to visualize the clathrin-binding loop and the 344-loop of the arrestin2 C-domain, which are not detected in the available crystal structures of apo arrestin2 [bovine: PDB 1G4M (Han et al., 2001), human: PDB 8AS4 (Isaikina et al., 2023)]. In the other structured regions, the model is virtually identical to the crystal structures”.

(6) Several figure panels were difficult to interpret due to their small size. Especially microscopy insets, where I needed to simply trust that the authors were accurately describing the data. Enlarging panels is essential, and this may require separating them into different figures.

We appreciate the referee’s concern regarding figure readability. However, we want to indicate that all our figures are provided as either high-resolution pixel or scalable vector graphics, which allow for zooming in to very fine detail, either electronically or in print. This ensures that microscopy insets and other small panels can be examined clearly when viewed appropriately. We believe the current layout of the figures is necessary to be able to efficiently compare the data between different conditions.

Many figure panels had text size that was too small. Font inconsistencies across figures also stand out. 

We apologize for this. We have now enlarged the font size in the figures and made the styles more consistent.

For Fig. 1F, consider adding individual data points and error bars.

Thank you for this suggestion. However, Figure 1F already contains the individual data points, with colored circles corresponding to the titration condition. As we did not have replicates of the titration, no error bars are shown. However, the close agreement of the theoretical fit with the individual measured data points stemming from different experiments shows that the statistical errors are indeed very small. We have estimated an overall error for the Kd (as indicated in panel F, right) by error propagation based on an estimate of the chemical shift error as obtained in the NMR software POKY (based on spectral noise). 

Reviewer #2 (Recommendations for the authors):

(1) I don't observe two overlapping spectra of Arrestin2 (1393) +/- CLTC NTD in Supplementary Figure 1.

As explained above all the spectra are shown as scalable vector graphics. The overlapping spectra are visible when zoomed in.

(2) I'd be tempted to move the discussion of class A and class B GPCRs and their presumed differences to the intro and then motivate the paper with specific questions.

We appreciate the referee’s suggestion and had a similar idea previously. However, as we do not have data on other class-A or class-B receptors, we rather don’t want to motivate the entire manuscript by this question.

Reviewer #3 (Recommendations for the authors): 

(1) What happens with full-length arr2 (1-418) when the phospho-peptide pp6 is added to the reaction? It's unclear to me that 1-418 would behave the same as 1-393 because the arr2 tail of 1-393 is likely sufficiently mobile to accommodate binding to CLTC NTD. I suggest attempting this experiment for added rigor.

We believe that there is a misunderstanding. The 1-393 and 1-418 constructs differ by the disordered C-terminal tail, which is not involved in the clathrin interaction with the arrestin2 376-380 (LIELD) residues. Accordingly, both 1-393 and 1-418 constructs show almost identical interactions with clathrin (Figure 2A and 2C). Moreover, the phospho-activated arrestin2^1-393 (Figure 2B) interacts identically with clathrin as inactive arrestin2^1-393 and inactive arrestin2^1-418. We believe that this comparison is sufficient for the conclusion that arrestin activation does not play a role in arrestin-clathrin binding.

(2) If the tags were moved to the N-terminus of the receptor and/or arr2, I wonder if the complex is as stable (Figure 4)? 

We thank the referee for their suggestion. We have indeed attempted to perform our experiments using an N-terminally SNAP-tagged CCR5. Unfortunately, this construct did not express in the HeLa cells indicating that SNAP-CCR5 was either toxic or degraded. Unfortunately, as the lab is closing due to the retirement of the PI, we are not able to repeat these experiments with further differently positioned tags. We refer also to our answer above that the experiments with the antagonist [5P12]CCL5 present a certain control.

(3) A biochemical assay to measure receptor internalization, in addition to the cell biological approach (Figure 5), would add additional rigor to the study and conclusions.

We tried to measure internalization using a biochemical approach. We tried to pull-down CCR5 from HeLa cells and assess arrestin binding. Unfortunately, even using different buffer conditions, we found that CCR5 was aggregating once solubilized from membranes, preventing us from doing this analysis. We had a similar problem when we exogenously expressed CCR5 in insect cells for purification purposes. We have long experience with CCR5, and this receptor is very aggregation-prone due to extended charged surfaces, which interact with the chemokines.

As an alternative, and in support of the cellular immunofluorescence assays, we also attempted to obtain internalization data via FACS using a CCR5 surface antibody (CD195 Monoclonal Antibody eBioT21/8). CD195 recognizes the N-terminus of the receptor. Unfortunately, the presence of the chemokine ligand (~ 8 kDa) interferes with antibody binding, precluding the quantitative biochemical assessment of the arrestin2 mutants on the CCR5 internalization.

For these reasons, we were particularly careful to quantify CCR5 internalization from the immunofluorescence microscopy data using colocalization coefficients as well as puncta counting (Figure 4+5).

eLife Assessment

In this manuscript Taujale et al describe an interdisciplinary approach to mine the human channelome and further discover orthologues across diverse organisms. Further, this work provides evidence that supports a role for conserved residues in CALHM channel gating. Overall this important work presents findings that can be helpful to the ion channel community, as well as to those interested in improved methods for mining sequence space for their protein of interest. However, further validation of the improvements their approach shows over previous approaches is needed, making this a solid contribution to the literature in this field.

Reviewer #1 (Public review):

Summary:

In the manuscript "Identification and classification of ion-channels across the tree of life: Insights into understudied CALHM channels" Taujale et al describe an interdisciplinary approach to mine the human channelome and further discover orthologues across diverse organisms, culminating in delineating co-conserved patterns in an example ion channel: CALHM. Overall, this paper comes in two sections, one where 419 human ion channels and 48,000+ channels from diverse organisms are found through a multidisciplinary data mining approach, and a second where this data is used to find co-conserved sequences, whose functional significance is validated via experiments on CALHM1 and CALHM6. Overall, this is an intriguing data-first approach to better understand even understudied ion channels like CALHM6. However, more needs to be done to pull this story together into a single coherent narrative.

Strengths:

This manuscript takes advantage of modern-day LLM tools to better mine the literature for ion channel sequences in humans and other species with orthologous ion channel sequences. They explore the 'dark channome' of understudied ion channels to better reveal the information evolution has to tell us about our own proteins, and illustrate the information this provides access to in experimental studies in the final section of the paper. Finally, they provide a wealth of information in the supplementary tables (in the form of Excel spreadsheets and a dataset on Zenodo) for others to explore. Overall, this is a creative approach to a wide-reaching problem that can be applied to other families of proteins.

Weaknesses:

Overall, while a considerable amount of work has been done for this manuscript, the presentation, both in terms of writing and figures, still can use more work even after a first round of revisions. While they have improved their discussion to more clearly describe the need for a better-curated sequence database of ion channels, and how existing resources fall short, some aspects of this process and the motivation remain unclear, especially when it comes to the CALHM sequences.

Overall, this manuscript is a valuable contribution to the field, but requires a few main things to make it truly useful. Namely, how has this approach really improved their ability to identify conserved residues in CALHM over a less-involved approach? And better organization of the first results section of the paper, which is critical to the downstream understanding of the paper, as well as some cosmetic improvements.

Reviewer #2 (Public review):

Summary:

In this paper, the authors defined the "channelome," consisting of 419 predicted human ion channels as well as 48,000 ion channel orthologs from other organisms. Using this information, the ion channels were clustered into groups, which can potentially be used to make predictions about understudied ion channels in the groups. The authors then focused on the CALHM ion channel family, mutating conserved residues and assessing channel function.

Strengths:

The curation of the channelome provides an excellent resource for researchers studying ion channels. Supplemental Table 1 is well organized with an abundance of useful information.

Comments on revisions:

The authors have thoroughly addressed my concerns and the manuscript is substantially improved. I have just a few suggestions regarding wording/clarification.

In Supplemental Figure 4, the Western blots (n=3) were quantitated, but the surface biotinylation was not. While I suppose that it is fine to just show one representative experiment for the biotinylation assay, the authors should indicate in the legend how many times this was done. It is essential to know whether these data in Supplemental Figure 4E, F are reproducible as they are absolutely critical for interpretation of all of the data in Figure 5.

Author response:

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

Reviewing Editor Comments:

(A) Revisions related to the first part, regarding data mining and curation:

(1) One question that arises with the part of the manuscript that discusses the identification and classification of ion channels is whether these will be made available to the wider public. For the 419 human sequences, making a small database to share this result so that these sequences can be easily searched and downloaded would be desirable. There are a variety of acceptable formats for this: GitHub/figshare/zenodo/university website that allows a wider community to access their hard work. Providing such a resource would greatly expand the impact of this paper. The same question can be asked of the 48,000+ ion channels from diverse organisms.

We thank the reviewer for providing this important feedback. While the long term plan is to provide access to these sequences and annotations through a knowledge base resource like Pharos, we agree with the comments that it would be beneficial to have these sequences made available with the manuscript as well. We have compiled 3 fasta files containing the following: 1) Full length sequences for the curated 419 ion channel sequences. 2) Pore containing domain sequences for the 343 pore domain containing human ion channel sequences. 3) All the identified orthologs for the human ion channels.

For each sequence in these files, we have extended the ID line to include the most pertinent annotation information to make it readily available. For example, the id>sp|P48995|TRPC1_HUMAN|TRP:VGIC--TRP-TRPC|pore-forming|dom:387-637 provides the classification, unit and domain bounds for the human TRPC1 in the fasta file itself.

These files have been uploaded to Zenodo and are available for download with doi 10.5281/zenodo.16232527. We have included this in the Data Availability statement of the manuscript as well.

(2) Regarding the 48,000+ sequences, what checks have been done to confirm that they all represent bona fide, full-length ion channel sequences? Uniprot contains a good deal of unreviewed sequences, especially from single-celled organisms. The process by which true orthologues were identified and extraneous hits discarded should be discussed in more detail, and all inclusion criteria should be described and justified, clearly illustrating that the risk of gene duplicates and fragments in this final set of ion channel orthologues has been avoided. Related to this, does this analysis include or exclude isoforms?

We thank the reviewer for raising this important point. Our selection of curated proteomes and the KinOrtho pipeline for orthology detection returns, up to an extent, reliable orthologous sequence sets. In brief, our database sequences are retrieved from full proteomes that only include proteins that are part of an official proteome release. Thus, they are mapped from a reference genome to ensure species-specific relevance and avoid redundancy. The >1500 proteomes in this analysis were selected based on their wider use in other orthology detection pipelines like OMA and InParanoid. Our orthology detection pipeline, KinOrtho, performs a fulllength and a domain-based orthology detection which ensures that the orthologous relationships are being defined based on the pore-domain sequence similarity. 

But we agree with the reviewer that this might leave room for extraneous, fragments or misannotated sequences to be included in our results. Taking this into careful consideration, we have expanded our sequence validation pipeline to include additional checks such as checking the uniport entry type, protein existence evidence and sequence level checks such as evaluating the compositional bias, non-standard codons and sequence lengths. These validation steps are now described in detail in the Methods section under orthology analysis (lines 768-808). All the originally listed orthologous sequences passed this validation pipeline and thus provide additional confidence that they are bona fide full length ion channel sequences.

We have also expanded this section (lines 758 – 766) to provide more details of the KinOrtho pipeline for orthology detection, which is a previously published method used for orthology detection in kinases by our lab.

Finally, our orthology analysis excludes isoforms and only spans the primary canonical sequences that are part of the UniProt Proteomes annotated sequence set. The isoforms that are generally available in UniProt Proteomes in a separate file named *_additional.fasta were not included in this analysis.

(3) The decision to show the families of ion channels in Figure 1 as pie charts within a UMAP embedding is intriguing but somewhat non-intuitive and difficult to understand. Illustrating these results with a standard tree-like visualization of the relationship of these channels to each other would be preferred.

We appreciate the feedback provided by the reviewer, and understand that a standard tree-like visualization would be much easier to interpret and familiar than a bubble chart based on UMAP embeddings. However, we opted to use the bubble chart for the following reasons:

Low sequence similarity: the 419 human ICs share very minimal sequence similarity, falling in the twilight zone or lower ( Dolittle, 1992; PMID:1339026). Thus, traditional multiple sequence alignment and phylogenetic reconstruction methods perform very poorly and generate unreliable or even misleading results. To explore the practicality of this option, we pursued performing a multiple sequence alignment of just 3 of the possibly related IC families as suggested by reviewer 2 (CALHM, Pannexins, and Connexins) using the state of the art structure based sequence alignment method Foldmason (doi: https://doi.org/10.1101/2024.08.01.606130). Even then, the sequence alignment and the resulting tree for just these 3 families were poor and unreliable, as illustrated in the attached Author response Image 2.

Protein embeddings based clustering: Novel LLM based approaches such as the protein language model embeddings offer ways to overcome these limitations by capturing sequence, structure, function and evolutionary properties in a high-dimensional space. Thus, we employed this model using DEDAL followed by UMAP for dimensionality reduction, which preserves biologically meaningful local and global relationships.

Abstraction at family level: In Figure 1, we aggregate individual channels into family bubbles with their positions representing the average UMAP coordinates of their members. This offers a balance between an intuitive view of how IC families are distributed in the embedding space and reflects potential functional and evolutionary proximities, while not being impeded by individual IC relationships across families.

We have revised the figure legend (lines 1221 – 1234) with additional description of the visualization and the process used to generate it, and the manuscript text (lines 248-270) provides the rationale behind the selection of this method.

(4) A strength of this paper is the visualization of 'dark' ion channels. However, throughout the paper, this could be emphasized more as the key advantage of this approach and how this or similar approaches could be used for other families of proteins. Specifically, in the initial statement describing 'light' vs 'dark channels', the importance of this distinction and the historical preference in science to study that which has already been studied can be discussed more, even including references to other studies that take this kind of approach. An example of a relevant reference here is to the Structural Genomics Consortium and its goals to achieve structures of proteins for which functions may not be well-characterized. Clarifying these motivations throughout the entire paper would strengthen it considerably.

We thank the reviewer for this constructive comment and agree that highlighting the strength of visualizing “dark” channels and prioritizing them for future studies would strengthen the paper. As suggested, we have revised the text throughout the paper (lines 84-89, 176-180) to contextualize and emphasize this distinction. We have also added a reference for the Structural Genomics Consortium, which, along with resources like IDG, has provided significant resources for prioritizing understudied proteins.

(5) Since the authors have generated the UMAP visualization of the channome, it would be interesting to understand how the human vs orthologue gene sets compare in this space.

We appreciate the reviewer’s input. It is an interesting idea to explore the UMAP embedding space for the human ICs along with their orthologs. The large number of orthologous sequences (>37,000) would certainly impose a computational challenge to generate embeddings-based pairwise alignments across all of them. Downstream dimensionality reduction from such a large set and the subsequent visualization would also suffer from accuracy and interpretability concerns. However, to follow up on the reviewer’s comments, we selected orthologous sequences from a subset of 12 model organisms spanning all taxa (such as mouse, zebrafish, fruit fly, C. elegans, A. thaliana, S. cerevisiae, E. coli, etc.).This increased the number of sequences for analysis to 1094 from 343, which is still manageable for UMAP. Using the exact same method, we generated the UMAP embeddings plot for this set as shown below. 

Author response image 1.

UMAP embeddings of the human ICs alongside orthologs from 12 model organisms

As shown above, we observed that each orthologous set forms tight, well-defined clusters, preserving local relationships among closely related sequences. For example, a large number of VGICs cluster more closely together compared to Supplementary Figure 1 (with only the human ICs). However, families that were previously distant from others now appear to be even more scattered or pushed further away, indicating a loss of global structure. This pattern suggests that while local distances are well preserved, the global topology of the embedding space could be compromised. Moreover, we find that the placement of ICs with respect to other families is highly sensitive to the parameter choices (e.g., n_neighbors and min_dist), an issue which we did not encounter when using only the human IC sequences. The inclusion of a large number of orthologous sequences that are highly similar to a single human IC but dissimilar to others skews the embedding space, emphasizing local structure at the expense of global relationships.

Since UMAP and similar dimensionality reduction methods prioritize local over global structure, the resulting embeddings accurately reflect strong ortholog clustering but obscure broader interfamily relationships. Consequently, interpreting the spatial arrangement of human IC families with respect to one another becomes unreliable. We have made this plot available as part of this response, and anyone interested can access this in the response document.   

(6) Figure 1 should say more clearly that this is an analysis of the human gene set and include more of the information in the text: 419 human ion channel sequences, 75 sequences previously unidentified, 4 major groups and 55 families, 62 outliers, etc. Clearer visualizations of these categories and numbers within the UMAP (and newly included tree) visualization would help guide the reader to better understand these results. Specifically, which are the 75 previously unidentified sequences?

We thank the reviewer for the comments. To address this, we have revised Figure 1 and added more information, including a clear header that states that these are only human IC sets, numbers showing the total number of ICs, and the number of ICs in each group. We have further included new Supplementary Figure 2 and Supplementary Table 2, which show the overlap of IC sequences across the different resources. Supplementary Figure 2 is an upset plot that provides a snapshot of the overlap between curated human ICs in this study compared to KEGG, GtoP, and Pharos. Supplementary Table 2 provides more details on this overlap by listing, for each human IC, whether they are curated as an IC in the 3 IC annotation resources. We believe these additions should provide all the information, including the unidentified sequences we are adding to this resource.

(7) Overall, the manuscript needs to provide a clearer description of the need for a better-curated sequence database of ion channels, as well as how existing resources fall short.

We thank the reviewer for pointing out this important gap in the description. As suggested, we have revised the text thoroughly in the Introduction section to address this comment. Specifically, we have added sections to describe existing resources at sequence and structure levels that currently provide details and/or classification of human ion channels. Then, we highlight the facts that these resources are missing some characterized pore-containing ICs, do not include any information on auxiliary channels, and lack a holistic evolutionary perspective, which raises the need for a better-curated database of ion channels. Please refer to lines 57-63, 73-79, and 95 – 119 for these changes and additions.

(8) Some of the analysis pipeline is unclear. Specifically, the RAG analysis seems critical, but it is unclear how this works - is it on top of the GPT framework and recursively inquires about the answer to prompts? Some example prompts would be useful to understand this.

We thank the reviewer for highlighting this gap in explanation. We understand that the details provided in the Methods and Supplementary Figure 1 may not have sufficiently explained the pipeline, and are missing some important details. The RAG pipeline leverages vector-based retrieval integrated with OpenAI’s GPT-4o model to systematically search literature and generate evidence-based answers. The process is as follows:

Literature sources (PubMed articles) relevant to the annotated ion channels were converted into vector representations stored in a Qdrant database.

Queries constructed from the annotated IC dataset were submitted to the vector database, retrieving contextually relevant literature segments.

Retrieved contexts served as inputs to the GPT-4o model, which produced structured JSON-formatted responses containing direct evidence regarding ion selectivity and gating mechanisms, along with associated confidence scores.

To clarify this further, we have rewritten the relevant subsection in lines 649 - 718. Now, this section provides a detailed description of the RAG pipeline. Also, we have improved Supplementary Figure 1 to provide a clearer description of the pipeline. We have also provided an example prompt template to illustrate the query. These additions clarify how the pipeline functions and demonstrate its practical utility for IC annotation.

(9) The existence of 76 auxiliary non-pore containing 'ion channel' genes in this analysis is a little confusing, as it seems a part of the pipeline is looking for pore-lining residues. Furthermore, how many of these are picked up in the larger orthologues search? Are these harder to perform checks on to ensure that they are indeed ion channel genes? A further discussion of the choice to include these auxiliary sequences would be relevant. This could just be further discussion of the literature that has decided to do this in the past.

We thank the reviewer for this comment, and agree that further clarification of our selection and definition of auxiliary IC sequences would be helpful. As the reviewer has pointed out, one of the annotation pipeline steps is indeed looking for the pore-lining residues. Any sequences that do not have a pore-containing domain are then considered to be auxiliary, and we search for additional evidence of their binding with one of the annotated pore-containing ICs. If such evidence is not found in the literature, we remove them from our curated IC list. 

In response to the above comment, we have revised the manuscript text to provide these details. In the Introduction section, we have added references to previous literature that have described auxiliary ICs and also pointed out that the existing ion channel resources do not account for such auxiliary channels (lines 73-79, 107-108,148-149). We have also expanded the Methods section to describe the selection and definition of auxiliary channels (lines 640-646).

With regards to the orthology analysis, since auxiliary channels do not have a pore domain, and our orthology pipeline requires a pore domain similarity search and hit, we did not include them in this part of the analysis. We have clarified the text in the Results section to ensure this is communicated properly throughout the manuscript (lines 212-215, 260-263). 

(10) Why are only evolutionary relationships between rat, mouse, and human shown in Figure 3A? These species are all close on the evolutionary timeline.

We thank the reviewer for this comment. Figure 3A currently provides a high-level evolutionary relationship across the 6 human CALHM members as a pretext for the pattern based Bayesian analysis. However, since this analysis is based on a wider set of orthologs that span taxa, we agree that a larger tree that includes more orthologs is warranted.

We have now revised Figure 3A to include an expanded tree that includes 83 orthologs from all 6 human CALHM members spanning 14 organisms from different taxa, ranging from mammals, fishes, birds, nematodes, and cnidarians. The overall structure of the tree is still consistent with 2 major clades as before, with CALHM 1 and 3 in the first clade and CALHM 2,4,5, and 6 in the second clade, with good branch support.

(B) Revisions related to the second part, regarding the analysis of CAHLM channel mutations:

(1) It would strengthen the manuscript if it included additional discussion and references to show that previous methods to analyze conserved residues in CALHM were significantly lacking. What results would previous methods give, and why was this not enough? Were there just not enough identified CALHM orthologues to give strong signals in conservation analysis? Also, the amino acid conservation between CLHM-1 and CALHM1 is extremely low. Thus, there are other CALHM orthologs that give strong signals in conservation analysis. There are ~6 papers that perform in-depth analysis of the role of conserved residues in the gating of CALHM channels (human and C. elegans) that were not cited (Ma et al, Am J Physiol Cell Physiol, 2025; Syrjanen et al, Nat Commun, 2023; Danielli et al, EMBO J, 2023; Kwon et al, Mol Cells, 2021; Tanis et al, Am J Physiol Cell Physiol, 2017; Tanis et al, J Neurosci, 2013; Ma et al, PNAS, 2013) - these data needs to be discussed in the context of the present work.

We thank the reviewer for the comment and agree that these are excellent studies that have advanced understanding of conserved residues in CALHM gating. While their analyses compared a limited set of sequences, focusing on residues conserved in specific CALHM homologs or species like C. elegans, our analysis encompasses thousands of sequences across the entire CALHM family, allowing us to identify residues conserved across all family members over evolution. We also coupled this sequence analysis with hypotheses derived from our published structural studies (Choi et al., Nature, 2019), which highlighted the NTH/S1 region as a critical element in channel gating. Based on this, we focused on evolutionarily conserved residues in the S1–S2 linker and at the interface of S1 with the rest of the TMD, reasoning that if S1 movement is essential for gating, these two structural elements (acting as a hinge and stabilizing interface, respectively) would be key determinants of the conformational dynamics of S1. These regions have been largely overlooked in previous studies. As a result, the residues highlighted in our study do not overlap with those previously reported but instead provide complementary insights into gating mechanisms in this unique channel family. Together, our study and the published literature suggest that many regions and residues in CALHM proteins are critical for gating: while some are conserved across the entire family evolutionarily, others appear conserved only within certain species or subfamilies.

To address the reviewer’s comment, and to highlight the points mentioned above, we have added a brief discussion of these studies and the relevant citations in the revised manuscript (lines 378– 385, 563–576).

(2) Whereas the current-voltage relations for WT channels are clearly displayed, the data that is shown for the mutants does not allow for determining if their gating properties are indeed different than WT.

First, the current amplitudes for the mutants were quantified at just one voltage, which makes it impossible to determine if their voltage-dependence was different than WT, which would be a strong indicator for an effect in gating. Current-voltage relations as done for the WT channels should be included for at least some key mutations, which should include additional relevant controls like the use of Gd3+ as an inhibitor to rule out the contribution of some endogenous currents.

We thank the reviewer for this comment. To address this, we performed additional experiments using a multi-step pulse protocol to obtain current-voltage relations for WT CALHM1, CALHM1(I109W), WT CALHM6, and CALHM6(W113A). Our initial two-step protocol (−80 mV and +120 mV) covers both the physiological voltage range and the extended range commonly used in biophysical characterization of ion channels. Most mutants did not exhibit channel activation even within this broad range. We therefore focused on the three mutants that did show substantial activation to perform full I–V analysis as suggested. In all groups, currents activated at 37 °C were significantly inhibited by Gd³⁺, consistent with published reports (Ma et al., AJP 2025; Danielli et al., EMBO J 2023; Syrjänen et al., Nat Commun 2023). Notably, for CALHM6(Y51A), while this mutation did not significantly alter current amplitudes at positive membrane potentials, it markedly reduced currents at negative potentials, rendering the channel outwardly rectifying and altering its voltage dependence. These new data are incorporated into Figure 5 (panels A–O) and discussed in the manuscript. Figure 5 now also shows current amplitudes at both +120 mV and −80 mV in 0 mM Ca²⁺ at 37 °C to facilitate direct comparison between WT and mutants. The previous data at 5 mM Ca²⁺ and 0 mM Ca²⁺ at 22 °C have been moved to Supplementary Figure 5 as requested.

Second, it is unclear whether the three experimental conditions (5 mM Ca²⁺, and 0 Ca²⁺, at 22 and 37C) were measured in the same cell in each experiment, or if they represent different experiments. This should be clarified. If measurements at each condition were done in the same experiment, direct comparison between the three conditions within each individual experiment could further help identify mutations with altered gating.

We thank the reviewer for pointing this out and apologize for the confusion. All three conditions (5 mM Ca²⁺ at 22 °C, 0 mM Ca²⁺ at 22 °C, and 0 mM Ca²⁺ at 37 °C) were sequentially measured in the same cell within each experiment. The currents were then averaged across cells and plotted for each group.

Third, in line 334, the authors state that "expression levels of wild-type proteins and mutants are comparable." However, Western blots showing CALHM protein abundance (Supplementary Fig. 3) are not of acceptable quality; in the top blot, WT CALHM1 appears too dim, representative blots were not shown for all mutants, and individual data points should be included on the group data quantitation of the blots, together with a statistical test comparing mutants with the WT control.

We thank the reviewer for the comment and agree that representative blots were not shown for all mutants. Supplementary Figure 4 (previously Supplementary Figure 3) has been updated to include representative blots for all mutants, individual data points in the quantification, and statistical tests comparing each mutant to the WT control.

A more serious concern is that the total protein quantitation is not very informative about the functional impact of mutations in ion channels, because mutations can severely impact channel localization in the plasma membrane without reducing the total protein that is translated. In mammalian cells, CALHM6 is localized to intracellular compartments and only translocates to the plasma membrane in response to an activating stimulus (Danielli et al, EMBO J, 2023). Thus, if CALHM6 is only intracellular, the protein amount would not change, but the measured current would. Abundant intracellular CALHM1 has also been observed in mammalian cells transfected with this protein (Dreses-Werringloer et al., Cell, 2008). Quantitation of surface-biotinylated channels would provide information on whether there are differences between the constructs in relation to surface expression rather than gating. An alternative approach to biotinylation would be to express GFP-tagged constructs in Xenopus oocytes and look for surface expression. This is what has been done in previous CALHM channel studies.

Without evidence for the absence of defects in localization or clear alterations in gating properties, it is not possible to conclude whether mutant channels have altered activity. Does the analysis of sequences provide any testable hypotheses about substitutions with different side chains at the same position in the sequence?

We thank the reviewer for this very important comment. We agree that total protein levels alone do not distinguish between intracellular retention and proper trafficking to the plasma membrane. To address this, we performed surface biotinylation assays for all WT and mutant CALHM1 and CALHM6 constructs to assess their plasma membrane localization. The results show that mutants have either comparable or substantially higher surface expression levels than WT, consistent with the Western blot data. Together, these findings support our original interpretation that the observed differences in electrophysiological currents are not due to trafficking defects but reflect functional effects. These new data are presented in Supplementary Figure 5.

(3) Line 303 - 13 aligned amino acids were conserved across all CALHM homologs - are these also aligned in related connexin and pannexin families? It is likely that cysteines and proline in TM2 are since CALHM channels overall share a lot of similarities with connexins and pannexins (Siebert et al, JBC, 2013). As in line 207, it would be expected that pannexins, connexins, and CALHM channel families would group together. Related to this, see Line 406 - in connexins, there is also a proline kink in TM2 that may play a role in mediating conformational changes between channel states (Ri et al, Biophysical Journal, 1999). This should be discussed.

We thank the reviewer for the suggestion. We attempted a structure based sequence alignment of representative structures from all 3 families (CALHM, connexins and pannexins), but the resulting alignments are very poor and have a lot of gapped regions, making it very difficult to comment on the similarities mentioned in this comment. This is actually expected, as although CALHM, connexins, and pannexins are all considered “large-pore” channels, the TMD arrangement and conformation of CALHM are distinct from those of connexins and pannexins. Below, we have included a snapshot of the alignment at the conserved cysteine regions of the CALHM homologs, along with the resulting tree, which has very low support values and has difficulty placing the connexins properly, making it difficult to interpret.

Author response image 2.

Structure based sequence alignment and phylogenetic analysis of available crystal structures of members from the CALHM, Pannexin and Connexin families. Top: The resulting sequence alignment is very sparse and does not show conservation of residues in the TM regions. The CPC motif with conserved cysteines in CALHM family is shown. Bottom: Phylogenetic tree based on the alignment has low support values making it difficult to interpret.

(4) Line 36 - This work does not have experimental evidence to show that the selected evolutionarily conserved residues alter gating functions.

Our electrophysiology data demonstrate that the selected evolutionarily conserved residues have a major impact on CALHM1 and CALHM6 gating. As shown in Figure 5, mutations at these residues produce two distinct phenotypes: (1) nonconductive channels, and (2) altered voltage dependence, resulting in outward rectification. Importantly, these functional changes occur despite normal total expression and surface trafficking, as confirmed by Western blotting and surface biotinylation (Supplementary Figure 4). These findings indicate that the affected residues are critical for the conformational dynamics underlying channel gating rather than for protein expression or localization.

(5) Line 296-297 - This could also be put in the context of what we already know about CALHM gating. While all cryo EM structures of CALHM channels are in the open state, we still do understand some things about gating mechanism (Tanis et al Am J Physiol Cell Physiol, Cell Physiol 2017; Ma et al Am J Physiol Cell Physiol, Cell Physiol 2025) with the NT modulating voltage dependence and stabilizing closed channel states and the voltage dependent gate being formed by proximal regions of TM1.

Thank you for providing this suggestion. As suggested, we have revised the text to place our findings in the context of current knowledge about CALHM gating and have added the relevant citations (lines 370-373).

(6) Lines 314-315 - Just because residues are conserved does not mean that they play a role in channel gating. These residues could also be important for structure, ion selectivity, etc.

We agree that evolutionary conservation alone does not imply a role in gating. However, our hypothesis derives from the positioning of these conserved residues, and previous studies that have indicated the importance of the NTH/S1 region for channel gating function. More importantly, our electrophysiology data indicate that these conserved residues specifically impact channel gating in CALHM1 and CALHM6. We have revised the text in lines 404-406 to clarify this further.

(7) Line 333 - while CALHM6 is less studied than CALHM1, there is knowledge of its function and gating properties. Should CALHM6 be considered a "dark" channel? The IDG development level in Pharos is Tbio. There have been multiple papers published on this channel (ex: Ebihara et al, J Exp Med, 2010; Kasamatsu et al, J Immunol 2014; Danielli et al, EMBO J, 2023).

We thank the reviewer for noting this important discrepancy. We have updated the text and labels related to CALHM6 to reflect its status as Tbio in the manuscript.

(8) Please cite Jeon et al., (Biochem Biophys Res Commun, 2021), who have already shown temperature-dependence of CALHM1.

Thank you for the comment. We have added the citation.  

(9) It would be helpful to have a schematic showing amino acid residues, TM domains, highlighted residues mutated, etc.

Thank you for the suggestion. We have revised the figure and added labels for the TM domains, and highlighted the mutated residues.

Reviewer #1 (Recommendations for the authors):

(1) Why in the title is 'ion-channels' hyphenated but in the text it is not?

This has been changed.

(2) Line 78: 'Cryo-EM' is not defined before the acronym is used.

This has been fixed.

(3) Typo in line 519: KinOrthto.

This has been fixed.

(4) Capitalizing 'Tree of Life' is a bit strange in section 2 of the results and the Discussion.

We have removed the capitalization as suggested.

(5) In Figure 3 and Supplementary Figure 4A, the gene names in the tree are CAHM and not CALHM - I assume this is an error.

This has been made consistent to CALHM.

(6) Font sizes throughout all figures, with the exception of Figure 1, need to be more legible. The X-axis labels in Figure 2A are hard to read, for example (though I can see that there is also the CAHM/CALHM typo here...). A good rule of thumb is that they should be the same size as the manuscript text. Furthermore, the grey backgrounds of Figure 4 and Figure 5 are off-putting; just having a white background here should be sufficient.

This has been addressed. We have increased the font size in all figures with these revisions. The styling for Figure 4 and 5 has also been made consistent with other figures.

Reviewer #2 (Recommendations for the authors):

(1) Line 36 - This work does not have experimental evidence to show that the selected evolutionarily conserved residues alter gating functions.

Addressed in comment #4 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(2) Line 168 - should also be Supplemental Table 1.

This has been addressed.

(3) Line 170 - 419 human ion channel sequences were identified and this was an increase of 75 sequences over previous number. Which 75 proteins are these?

This is now shown in Supplementary Figure 2 and Supplementary Table 2. Supplementary Figure 2 shows an Upset plot with the number of sequences that overlap across databases and the novel sequences that we have added as part of this study. The 75 specifically refers to the sequences that were not included in Pharos, which was chosen to refer to this number since it has the highest number of ICs listed out of all the other resources. Further, Supplementary Table 2 now provides a list of individual ICs and whether they were present in each of the 3 databases compared.

(4) Line 289 - Ca2+ (not Ca); other similar mistakes throughout the manuscript

These have been fixed.

(5) Line 291-292 - Please include more about functions for CALHM channels; ex. CALHM1 regulates cortical neuron excitability (Ma et al, PNAS 2012), CLHM-1 regulates locomotion and induces neurodegeneration in C. elegans (Tanis et al. Journal of Neuroscience 2013); see above for references on CALHM6 function.

We have added the functions as suggested.

(6) Line 296-297 - This could also be put in the context of what we already know about CALHM gating. While all cryo EM structures of CALHM channels are in the open state, we still do understand some things about gating mechanism (Tanis et al Am J Physiol Cell Physiol, Cell Physiol 2017; Ma et al Am J Physiol Cell Physiol, Cell Physiol 2025) with the NT modulating voltage dependence and stabilizing closed channel states and the voltage dependent gate being formed by proximal regions of TM1.

Addressed in comment #5 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(7) Lines 314-315 - Just because residues are conserved does not mean that they play a role in channel gating. These residues could also be important for structure, ion selectivity, etc.

Addressed in comment #6 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(8) Line 333 - While CALHM6 is less studied than CALHM1, there is knowledge of its function and gating properties. Should CALHM6 be considered a "dark" channel? The IDG development level in Pharos is Tbio. There have been multiple papers published on this channel (ex: Ebihara et al, J Exp Med, 2010; Kasamatsu et al, J Immunol 2014; Danielli et al, EMBO J, 2023).

Addressed in comment #7 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(9) Line 627 - Do you mean that 5 mM CaCl2 was replaced with 5 mM EGTA in 0 Ca2+ solution?

This is correct.  

(10) Why are only evolutionary relationships between rat, mouse, and human shown in Figure 3A? These species are all close on the evolutionary timeline.

Addressed in comment #10 for Part A Revisions related to the first part, regarding data mining and curation above.

(11) Figure 5 - no need to show the currents at room temperature in the main text since there are robust currents at 37 degrees; this could go into the supplement. Also, please cite Jeon et al. (Biochem Biophys Res Commun, 2021), who have already shown temperature-dependence of CALHM1.

Addressed in comment #8 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(12) It would be helpful to have a schematic showing amino acid residues, TM domains, highlighted residues mutated etc.

Addressed in comment #9 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(13) Use of S1-S4 to refer to the transmembrane "segments" is not standard; rather, TM1-TM4 would generally be used to refer to transmembrane domains.

We have used the S1–S4 helix notation to maintain consistency with the nomenclature employed in our previous study (Choi et al., Nature, 2019).

Author Response:

Reviewer #1 (Public Review):

[...] The major limitation of the manuscript lies in the framing and interpretation of the results, and therefore the evaluation of novelty. Authors claim for an important and unique role of beliefs-of-other-pain in altruistic behavior and empathy for pain. The problem is that these experiments mainly show that behaviors sometimes associated with empathy-for-pain can be cognitively modulated by changing prior beliefs. To support the notion that effects are indeed relating to pain processing generally or empathy for pain specifically, a similar manipulation, done for instance on beliefs about the happiness of others, before recording behavioural estimation of other people's happiness, should have been performed. If such a belief-about-something-else-than-pain would have led to similar results, in terms of behavioural outcome and in terms of TPJ and MFG recapitulating the pattern of behavioral responses, we would know that the results reflect changes of beliefs more generally. Only if the results are specific to a pain-empathy task, would there be evidence to associate the results to pain specifically. But even then, it would remain unclear whether the effects truly relate to empathy for pain, or whether they may reflect other routes of processing pain.

We thank Reviewer #1's for these comments/suggestions regarding the specificity of belief effects on brain activity involved in empathy for pain. Our paper reported 6 behavioral/EEG/fMRI experiments that tested effects of beliefs of others’ pain on empathy and monetary donation (an empathy-related altruistic behavior). We showed not only behavioral but also neuroimaging results that consistently support the hypothesis of the functional role of beliefs of others' pain in modulations of empathy (based on both subjective and objective measures as clarified in the revision) and altruistic behavior. We agree with Reviewer 1# that it is important to address whether the belief effect is specific to neural underpinnings of empathy for pain or is general for neural responses to various facial expressions such as happy, as suggested by Reviewer #1. To address this issue, we conducted an additional EEG experiment (which can be done in a limited time in the current situation), as suggested by Reviewer #1. This new EEG experiment tested (1) whether beliefs of authenticity of others’ happiness influence brain responses to perceived happy expressions; (2) whether beliefs of happiness modulate neural responses to happy expressions in the P2 time window as that characterized effects of beliefs of pain on ERPs.

Our behavioral results in this experiment (as Supplementary Experiment 1 reported in the revision) showed that the participants reported less feelings of happiness when viewing actors who simulate others' smiling compared to when viewing awardees who smile due to winning awards (see the figure below). Our ERP results in Supplementary Experiment 1 further showed that lack of beliefs of authenticity of others’ happiness (e.g., actors simulate others' happy expressions vs. awardees smile and show happy expressions due to winning an award) reduced the amplitudes of a long-latency positive component (i.e., P570) over the frontal region in response to happy expressions. These findings suggest that (1) there are possibly general belief effects on subjective feelings and brain activities in response to facial expressions; (2) beliefs of others' pain or happiness affect neural responses to facial expressions in different time windows after face onset; (3) modulations of the P2 amplitude by beliefs of pain may not be generalized to belief effects on neural responses to any emotional states of others. We reported the results of this new ERP experiment in the revision as Supplementary Experiment 1 and also discussed the issue of specificity of modulations of empathic neural responses by beliefs of others' pain in the revised Discussion (page 49-50).

Supplementary Experiment Figure 1. EEG results of Supplementary Experiment 1. (a) Mean rating scores of happy intensity related to happy and neutral expressions of faces with awardee or actor/actress identities. (b) ERPs to faces with awardee or actor/actress identities at the frontal electrodes. The voltage topography shows the scalp distribution of the P570 amplitude with the maximum over the central/parietal region. (c) Mean differential P570 amplitudes to happy versus neutral expressions of faces with awardee or actor/actress identities. The voltage topographies illustrate the scalp distribution of the P570 difference waves to happy (vs. neutral) expressions of faces with awardee or actor/actress identities, respectively. Shown are group means (large dots), standard deviation (bars), measures of each individual participant (small dots), and distribution (violin shape) in (a) and (c).

In the revised Introduction we cited additional literatures to explain the concept of empathy, behavioral and neuroimaging measures of empathy, and how, similar to previous research, we studied empathy for others' pain using subjective (self reports) and objective (brain responses) estimation of empathy (page 6-7). In particular, we mentioned that subjective estimation of empathy for pain depends on collection of self-reports of others' pain and ones' own painful feelings when viewing others' suffering. Objective estimation of empathy for pain relies on recording of brain activities (using fMRI, EEG, etc.) that differentially respond to painful or non-painful stimuli applied to others. fMRI studies revealed greater activations in the ACC, AI, and sensorimotor cortices in response to painful or non-painful stimuli applied to others. EEG studies showed that event-related potentials (ERPs) in response to perceived painful stimulations applied to others' body parts elicited neural responses that differentiated between painful and neutral stimuli over the frontal region as early as 140 ms after stimulus onset (Fan and Han, 2008; see Coll, 2018 for review). Moreover, the mean ERP amplitudes at 140–180 ms predicted subjective reports of others' pain and ones' own unpleasantness. Particularly related to the current study, previous research showed that pain compared to neutral expressions increased the amplitude of the frontal P2 component at 128–188 ms after stimulus onset (Sheng and Han, 2012; Sheng et al., 2013; 2016; Han et al., 2016; Li and Han, 2019) and the P2 amplitudes in response to others' pain expressions positively predicted subjective feelings of own unpleasantness induced by others' pain and self-report of one's own empathy traits (e.g., Sheng and Han, 2012). These brain imaging findings indicate that brain responses to others' pain can (1) differentiate others' painful or non-painful emotional states to support understanding of others' pain and (2) predict subjective feelings of others' pain and one's own unpleasantness induced by others' pain to support sharing of others' painful feelings. These findings provide effective subjective and objective measures of empathy that were used in the current study to investigate neural mechanisms underlying modulation of empathy and altruism by beliefs of others’ pain.

In addition, we took Reviewer #1’s suggestion for VPS analyses which examined specifically how neural activities in the empathy-related regions identified in the previous research (Krishnan et al., 2016, eLife) were modulated by beliefs of others’ pain. The results (page 40) provide further evidence for our hypothesis. We also reported new results of RSA analyses(page 39) that activities in the brain regions supporting affective sharing (e.g., insula), sensorimotor resonance (e.g., post-central gyrus), and emotion regulation (e.g., lateral frontal cortex) provide intermediate mechanisms underlying modulations of subjective feelings of others' pain intensity due to lack of BOP. We believe that, putting all these results together, our paper provides consistent evidence that empathy and altruistic behavior are modulated by BOP.

Reviewer #2 (Public Review):

[...] 1. In laying out their hypotheses, the authors write, "The current work tested the hypothesis that BOP provides a fundamental cognitive basis of empathy and altruistic behavior by modulating brain activity in response to others' pain. Specifically, we tested predictions that weakening BOP inhibits altruistic behavior by decreasing empathy and its underlying brain activity whereas enhancing BOP may produce opposite effects on empathy and altruistic behavior." While I'm a little dubious regarding the enhancement effects (see below), a supporting assumption here seems to be that at baseline, we expect that painful expressions reflect real pain experience. To that end, it might be helpful to ground some of the introduction in what we know about the perception of painful expressions (e.g., how rapidly/automatically is pain detected, do we preferentially attend to pain vs. other emotions, etc.).

Thanks for this suggestion! We included additional details about previous findings related to processes of painful expressions in the revised Introduction (page 7-8). Specifically, we introduced fMRI and ERP studies of pain expressions that revealed structures and temporal procedure of neural responses to others' pain (vs. neutral) expressions. Moreover, neural responses to others' pain (vs. neutral) expressions were associated with self-report of others' feelings, indicating functional roles of pain-expression induced brain activities in empathy for pain.

1. For me, the key takeaway from this manuscript was that our assessment of and response to painful expressions is contextually-sensitive - specifically, to information reflecting whether or not targets are actually in pain. As the authors state it, "Our behavioral and neuroimaging results revealed critical functional roles of BOP in modulations of the perception-emotion-behavior reactivity by showing how BOP predicted and affected empathy/empathic brain activity and monetary donations. Our findings provide evidence that BOP constitutes a fundamental cognitive basis for empathy and altruistic behavior in humans." In other words, pain might be an incredibly socially salient signal, but it's still easily overridden from the top down provided relevant contextual information - you won't empathize with something that isn't there. While I think this hypothesis is well-supported by the data, it's also backed by a pretty healthy literature on contextual influences on pain judgments (including in clinical contexts) that I think the authors might want to consider referencing (here are just a few that come to mind: Craig et al., 2010; Twigg et al., 2015; Nicolardi et al., 2020; Martel et al., 2008; Riva et al., 2015; Hampton et al., 2018; Prkachin & Rocha, 2010; Cui et al., 2016).

Thanks for this great suggestion! Accordingly, we included an additional paragraph in the revised Discussion regarding how social contexts influence empathy and cited the studies mentioned here (page 46-47).

1. I had a few questions regarding the stimuli the authors used across these experiments. First, just to confirm, these targets were posing (e.g., not experiencing) pain, correct? Second, the authors refer to counterbalancing assignment of these stimuli to condition within the various experiments. Was target gender balanced across groups in this counterbalancing scheme? (e.g., in Experiment 1, if 8 targets were revealed to be actors/actresses in Round 2, were 4 female and 4 male?) Third, were these stimuli selected at random from a larger set, or based on specific criteria (e.g., normed ratings of intensity, believability, specificity of expression, etc.?) If so, it would be helpful to provide these details for each experiment.

We'd be happy to clarify these questions. First, photos of faces with pain or neutral expressions were adopted from the previous work (Sheng and Han, 2012). Photos were taken from models who were posing but not experience pain. These photos were taken and selected based on explicit criteria of painful expressions (i.e., brow lowering, orbit tightening, and raising of the upper lip; Prkachin, 1992). In addition, the models' facial expressions were validated in independent samples of participants (see Sheng and Han, 2012). Second, target gender was also balanced across groups in this counterbalancing scheme. We also analyzed empathy rating score and monetary donations related to male and female target faces and did not find any significant gender effect (see our response to Point 5 below). Third, because the face stimuli were adopted from the previous work and the models' facial expressions were validated in independent samples of participants regarding specificity of expression, pain intensity, etc (Sheng and Han, 2012), we did not repeat these validation in our participants. Most importantly, we counterbalanced the stimuli in different conditions so that the stimuli in different conditions (e.g., patient vs. actor/actress conditions) were the same across the participants in each experiment. The design like this excluded any potential confound arising from the stimuli themselves.

1. The nature of the charitable donation (particularly in Experiment 1) could be clarified. I couldn't tell if the same charity was being referenced in Rounds 1 and 2, and if there were multiple charities in Round 2 (one for the patients and one for the actors).

Thanks for this comment! Yes, indeed, in both Rounds 1 and 2, the participants were informed that the amount of one of their decisions would be selected randomly and donated to one of the patients through the same charity organization (we clarified these in the revised Method section, page 55-56). We made clear in the revision that after we finished all the experiments of this study, the total amount of the participants' donations were subject to a charity organization to help patients who suffer from the same disease after the study.

1. I'm also having a hard time understanding the authors' prediction that targets revealed to truly be patients in the 2nd round will be associated with enhanced BOP/altruism/etc. (as they state it: "By contrast, reconfirming patient identities enhanced the coupling between perceived pain expressions of faces and the painful emotional states of face owners and thus increased BOP.") They aren't in any additional pain than they were before, and at the outset of the task, there was no reason to believe that they weren't suffering from this painful condition - therefore I don't see why a second mention of their pain status should increase empathy/giving/etc. It seems likely that this is a contrast effect driven by the actor/actress targets. See the Recommendations for the Authors for specific suggestions regarding potential control experiments. (I'll note that the enhancement effect in Experiment 2 seems more sensible - here, the participant learns that treatment was ineffective, which may be painful in and of itself.)

Thanks for comments on this important point! Indeed, our results showed that reassuring patient identities in Experiment 1 or by noting the failure of medical treatment related to target faces in Experiment 2 increased rating scores of others' pain and own unpleasantness and prompted more monetary donations to target faces. The increased empathy rating scores and monetary donations might be due to that repeatedly confirming patient identity or knowing the failure of medical treatment increased the belief of authenticity of targets' pain and thus enhanced empathy. However, repeatedly confirming patient identity or knowing the failure of medical treatment might activate other emotional responses to target faces such as pity or helplessness, which might also influence altruistic decisions. We agree with Reviewer #2 that, although our subjective estimation of empathy in Exp. 1 and 2 suggested enhanced empathy in the 2nd_round test, there are alternative interpretations of the results and these should be clarified in future work. We clarified these points in the revised Discussion (page 41-42).

1. I noted that in the Methods for Experiment 3, the authors stated "We recruited only male participants to exclude potential effects of gender difference in empathic neural responses." This approach continues through the rest of the studies. This raises a few questions. Are there gender differences in the first two studies (which recruited both male and female participants)? Moreover, are the authors not concerned about target gender effects? (Since, as far as I can tell, all studies use both male and female targets, which would mean that in Experiments 3 and on, half the targets are same-gender as the participants and the other half are other-gender.) Other work suggests that there are indeed effects of target gender on the recognition of painful expressions (Riva et al., 2011).

Thanks for raising this interesting question! Therefore, we reanalyzed data in Exp. 1 by including participants' gender or face gender as an independent variable. The three-way ANOVAs of pain intensity scores and amounts of monetary donations with Face Gender (female vs. male targets) × Test Phase (1st vs. 2nd_round) × Belief Change (patient-identity change vs. patient-identity repetition) did not show any significant three-way interaction (F(1,59) = 0.432 and 0.436, p = 0.514 and 0.512, ηp2 = 0.007 and 0.007, 90% CI = (0, 0.079) and (0, 0.079), indicating that face gender do not influence the results (see the figure below). Similarly, the three-way ANOVAs with Participant Gender (female vs. male participants) × Test Phase × Belief Change did not show any significant three-way interaction (F(1,58) = 0.121 and 1.586, p = 0.729 and 0.213, ηp2 = 0.002 and 0.027, 90% CI = (0, 0.055) and (0, 0.124), indicating no reliable difference in empathy and donation between men and women. It seems that the measures of empathy and altruistic behavior in our study were not sensitive to gender of empathy targets and participants' sexes.

Figure legend: (a) Scores of pain intensity and amount of monetary donations are reported separately for male and female target faces. (b) Scores of pain intensity and amount of monetary donations are reported separately for male and female participants.

1. I was a little unclear on the motivation for Experiment 4. The authors state "If BOP rather than other processes was necessary for the modulation of empathic neural responses in Experiment 3, the same manipulation procedure to assign different face identities that do not change BOP should change the P2 amplitudes in response to pain expressions." What "other processes" are they referring to? As far as I could tell, the upshot of this study was just to demonstrate that differences in empathy for pain were not a mere consequence of assignment to social groups (e.g., the groups must have some relevance for pain experience). While the data are clear and as predicted, I'm not sure this was an alternate hypothesis that I would have suggested or that needs disconfirming.

Thanks for this comment! We feel sorry for not being able to make clear the research question in Exp. 4. In the revised Results section (page 27-28) we clarified that the learning and EEG recording procedures in Experiment 3 consisted of multiple processes, including learning, memory, identity recognition, assignment to social groups, etc. The results of Experiment 3 left an open question of whether these processes, even without BOP changes induced through these processes, would be sufficient to result in modulation of the P2 amplitude in response to pain (vs. neutral) expressions of faces with different identities. In Experiment 4 we addressed this issue using the same learning and identity recognition procedures as those in Experiment 3 except that the participants in Experiment 4 had to learn and recognize identities of faces of two baseball teams and that there is no prior difference in BOP associated with faces of beliefs of the two baseball teams. If the processes involved in the learn and reorganization procedures rather than the difference in BOP were sufficient for modulation of the P2 amplitude in response to pain (vs. neutral) expressions of faces, we would expect similar P2 modulations in Experiments 4 and 3. Otherwise, the difference in BOP produced during the learning procedure was necessary for the modulation of empathic neural responses, we would not expect modulations of the P2 amplitude in response to pain (vs. neutral) expressions in Experiment 4. We believe that the goal and rationale of Exp. 4 are clear now.

Author Response:

We thank the editors and the reviewers for their careful reading and rigorous evaluation of our manuscript. We thank them for their positive comments and constructive feedback, which led us to add further lines of evidence in support of our central hypothesis that intrinsic neuronal resonance could stabilize heterogeneous grid-cell networks through targeted suppression of low-frequency perturbations. In the revised manuscript, we have added a physiologically rooted mechanistic model for intrinsic neuronal resonance, introduced through a slow negative feedback loop. We show that stabilization of patterned neural activity in a heterogeneous continuous attractor network (CAN) model could be achieved with this resonating neuronal model. These new results establish the generality of the stabilizing role of neuronal resonance in a manner independent of how resonance was introduced. More importantly, by specifically manipulating the feedback time constant in the neural dynamics, we establish the critical role of the slow kinetics of the negative feedback loop in stabilizing network function. These results provide additional direct lines of evidence for our hypothesis on the stabilizing role of resonance in the CAN model employed here. Intuitively, we envisage intrinsic neuronal resonance as a specific cellular-scale instance of a negative feedback loop. The negative feedback loop is a well-established network motif that acts as a stabilizing agent and suppresses the impact of internal and external perturbations in engineering applications and biological networks.

Reviewer #1 (Public Review):

The authors succeed in conveying a clear and concise description of how intrinsic heterogeneity affects continuous attractor models. The main claim, namely that resonant neurons could stabilize grid-cell patterns in medial entorhinal cortex, is striking.

We thank the reviewer for their time and effort in evaluating our manuscript, and for their rigorous evaluation and positive comments on our study.

I am intrigued by the use of a nonlinear filter composed of the product of s with its temporal derivative raised to an exponent. Why this particular choice? Or, to be more specific, would a linear bandpass filter not have served the same purpose?

Please note that the exponent was merely a mechanism to effectively tune the resonance frequency of the resonating neuron. In the revised manuscript, we have introduced a new physiologically rooted means to introduce intrinsic neuronal resonance, thereby confirming that network stabilization achieved was independent of the formulation employed to achieve resonance.

The magnitude spectra are subtracted and then normalized by a sum. I have slight misgivings about the normalization, but I am more worried that, as no specific formula is given, some MATLAB function has been used. What bothers me a bit is that, depending on how the spectrogram/periodogram is computed (in particular, averaged over windows), one would naturally expect lower frequency components to be more variable. But this excess variability at low frequencies is a major point in the paper.

We have now provided the specific formula employed for normalization as equation (16) of the revised manuscript. We have also noted that this was performed to account for potential differences in the maximum value of the homogeneous vs. heterogeneous spectra. The details are provided in the Methods subsection “Quantitative analysis of grid cell temporal activity in the spectral domain” of the revised manuscript. Please note that what is computed is the spectra of the entire activity pattern, and not a periodogram or a scalogram. There was no tiling of the time-frequency plane involved, thus eliminating potential roles of variables there on the computation here.

In addition to using variances of normalized differences to quantify spectral distributions, we have also independently employed octave-based analyses (which doesn’t involve normalized differences) to strengthen our claims about the impact of heterogeneities and resonance on different bands of frequency. These octave-based analyses also confirm our conclusions on the impact of heterogeneities and neuronal resonance on low-frequency components.

Finally, we would like to emphasize that spectral computations are the same for different networks, with networks designed in such a way that there was only one component that was different. For instance, in introducing heterogeneities, all other parameters of the network (the specific trajectory, the seed values, the neural and network parameters, the connectivity, etc.) remained exactly the same with the only difference introduced being confined to the heterogeneities. Computation of the spectral properties followed identical procedures with activity from individual neurons in the two networks, and comparison was with reference to identically placed neurons in the two networks. Together, based on the several routes to quantifying spectral signatures, based on the experimental design involved, and based on the absence of any signal-specific tiling of the time-frequency plane, we argue that the impact of heterogeneities or the resonators on low-frequency components is not an artifact of the analysis procedures.

We thank the reviewer for raising this issue, as it helped us to elaborate on the analysis procedures employed in our study.

Which brings me to the main thesis of the manuscript: given the observation of how heterogeneities increase the variability in the low temporal frequency components, the way resonant neurons stabilize grid patterns is by suppressing these same low frequency components.

I am not entirely convinced that the observed correlation implies causality. The low temporal frequeny spectra are an indirect reflection of the regularity or irregularity of the pattern formation on the network, induced by the fact that there is velocity coupling to the input and hence dynamics on the network. Heterogeneities will distort the pattern on the network, that is true, but it isn't clear how introducing a bandpass property in temporal frequency space affects spatial stability causally.

Put it this way: imagine all neurons were true oscillators, only capable of oscillating at 8 Hz. If they were to synchronize within a bump, one will have the field blinking on and off. Nothing wrong with that, and it might be that such oscillatory pattern formation on the network might be more stable than non-oscillatory pattern formation (perhaps one could even demonstrate this mathematically, for equivalent parameter settings), but this kind of causality is not what is shown in the manuscript.

The central hypothesis of our study was that intrinsic neuronal resonance could stabilize heterogeneous grid-cell networksthrough targeted suppression of low-frequency perturbations.

In the revised manuscript, we present the following lines of evidence in support of this hypothesis (mentioned now in the first paragraph of the discussion section of the revised manuscript):

1. Neural-circuit heterogeneities destabilized grid-patterned activity generation in a 2D CAN model (Figures 2–3).

2. Neural-circuit heterogeneities predominantly introduced perturbations in the lowfrequency components of neural activity (Figure 4).

3. Targeted suppression of low-frequency components through phenomenological (Figure 5C) or through mechanistic (new Figure 9D) resonators resulted in stabilization of the heterogeneous CAN models (Figure 8 and new Figure 11). We note that the stabilization was achieved irrespective of the means employed to suppress low-frequency components: an activity-independent suppression of low-frequencies (Figure 5) or an activity-dependent slow negative feedback loop (new Figure 9).

4. Changing the feedback time constant τm in mechanistic resonators, without changes to neural gain or the feedback strength allowed us to control the specific range of frequencies that would be suppressed. Our analyses showed that a slow negative feedback loop, which results in targeted suppression of low-frequency components, was essential in stabilizing grid-patterned activity (new Figure 12). As the slow negative feedback loop and the resultant suppression of low frequencies mediates intrinsic resonance, these analyses provide important lines of evidence for the role of targeted suppression of low frequencies in stabilizing grid patterned activity.

5. We demonstrate that the incorporation of phenomenological (Figure 13A–C) or mechanistic (new Figure panels 13D–F) resonators specifically suppressed lower frequencies of activity in the 2D CAN model.

6. Finally, the incorporation of resonance through a negative feedback loop allowed us to link our analyses to the well-established role of network motifs involving negative feedback loops in inducing stability and suppressing external/internal noise in engineering and biological systems. We envisage intrinsic neuronal resonance as a cellular-scale activitydependent negative feedback mechanism, a specific instance of a well-established network motif that effectuates stability and suppresses perturbations across different networks (Savageau, 1974; Becskei and Serrano, 2000; Thattai and van Oudenaarden, 2001; Austin et al., 2006; Dublanche et al., 2006; Raj and van Oudenaarden, 2008; Lestas et al., 2010; Cheong et al., 2011; Voliotis et al., 2014). A detailed discussion on this important link to the stabilizing role of this network motif, with appropriate references to the literature is included in the new discussion subsection “Slow negative feedback: Stability, noise suppression, and robustness”.

We thank the reviewer for their detailed comments. These comments helped us to introducing a more physiologically rooted mechanistic form of resonance, where we were able to assess the impact of slow kinetics of negative feedback on network stability, thereby providing more direct lines of evidence for our hypothesis. This also allowed us to link resonance to the wellestablished stability motif: the negative feedback loop. We also note that our analyses don’t employ resonance as a route to introducing oscillations in the network, but as a means for targeted suppression of low-frequency perturbations through a negative feedback loop. Given the strong quantitative links of negative feedback loops to introducing stability and suppressing the impact of perturbations in engineering applications and biological networks, we envisage intrinsic neuronal resonance as a stability-inducing cellular-scale activity-dependent negative feedback mechanism.

Reviewer #2 (Public Review):

[...] The pars construens demonstrates that similar networks, but comprised of units with different dynamical behavior, essentially amputated of their slowest components, do not suffer from the heterogeneities - they still produce grids. This part proceeds through 3 main steps: a) defining "resonator" units as model neurons with amputated low frequencies (Fig. 5); b) showing that inserted into the same homogeneous CAN network, "resonator" units produce the same grids as "integrator" units (Figs. 6,7); c) demonstrating that however the network with "resonator" units is resistant to heterogeneities (Fig. 8). Figs. 9 and 10 help understand what has produced the desired grid stabilization effect. This second part is on the whole also well structured, and its step c) is particularly convincing.

We thank the reviewer for their time and effort in evaluating our manuscript, and for their rigorous evaluation and positive comments on our study.

Step b) intends to show that nothing important changes, in grid pattern terms, if one replaces the standard firing rate units with the ad hoc defined units without low frequency behavior. The exact outcome of the manipulation is somewhat complex, as shown in Figs. 6 and 7, but it could be conceivably summed up by stating that grids remain stable, when low frequencies are removed. What is missing, however, is an exploration of whether the newly defined units, the "resonators", could produce grid patterns on their own, without the CAN arising from the interactions between units, just as a single-unit effect. I bet they could, because that is what happens in the adaptation model for the emergence of the grid pattern, which we have studied extensively over the years. Maybe with some changes here and there, but I believe the CAN can be disposed of entirely, except to produce a common alignment between units, as we have shown.

Step a), finally, is the part of the study that I find certainly not wrong, but somewhat misleading. Not wrong, because what units to use in a model, and what to call them, is a legitimate arbitrary choice of the modelers. Somewhat misleading, because the term "resonator" evokes a more specific dynamical behavior that than obtained by inserting Eqs. (8)-(9) into Eq. (6), which amounts to a brute force amputation of the low frequencies, without any real resonance to speak of. Unsurprisingly, Fig. 5, which is very clear and useful, does not show any resonance, but just a smooth, broad band-pass behavior, which is, I stress legitimately, put there by hand. A very similar broad band-pass would result from incorporating into individual units a model of firing rate adaptation, which is why I believe the "resonator" units in this study would generate grid patterns, in principle, without any CAN.

We thank the reviewer for these constructive comments and questions, as they were extremely helpful in (i) formulating a new model for rate-based resonating neurons that is more physiologically rooted; (ii) demonstrating the stabilizing role of resonance irrespective of model choices that implemented resonance; and (iii) mechanistically exploring the impact of targeted suppression of low frequency components in neural activity. We answer these comments of the reviewer in two parts, the first addressing other models for grid-patterned activity generation and the second addressing the reviewer’s comment on “brute force amputation of the low frequencies” in the resonator neuron presented in the previous version of our manuscript.

I. Other models for grid-patterned activity generation.

In the adaptation model (Kropff and Treves, 2008; Urdapilleta et al., 2017; Stella et al., 2020), adaptation in conjunction with place-cell inputs, Hebbian synaptic plasticity, and intrinsic plasticity (in gain and threshold) to implement competition are together sufficient for the emergence of the grid-patterned neural activity. However, the CAN model that we chose as the substrate for assessing the impact of neural circuit heterogeneities on functional stability is not equipped with the additional components (place-cell inputs, synaptic/intrinsic plasticity). Therefore, we note that decoupling the single unit (resonator or integrator) from the network does not yield grid-patterned activity.

However, we do agree that a resonator neuron endowed with additional components from the adaptation model would be sufficient to elicit grid-patterned neural activity. This is especially clear with the newly introduced mechanistic model for resonance through a slow feedback loop (Figure 9). Specifically, resonating conductances such as HCN and M-type potassium channels can effectuate spike-frequency adaptation. One of the prominent channels that is implicated in introducing adaptation, the calcium-activated potassium channels implement a slow activitydependent negative feedback loop through the slow calcium kinetics. Neural activity drives calcium influx, and the slow kinetics of the calcium along with the channel-activation kinetics drive a potassium current that completes a negative feedback loop that inhibits neural activity. Consistently, one of the earliest-reported forms of electrical resonance in cochlear hair cells was shown to be mediated by calcium-activated potassium channels (Crawford and Fettiplace, 1978, 1981; Fettiplace and Fuchs, 1999). Thus, adaptation realized as a slow negative-feedback loop, in conjunction with place-cell inputs and intrinsic/synaptic plasticity would elicit gridpatterned neural activity as demonstrated earlier (Kropff and Treves, 2008; Urdapilleta et al., 2017; Stella et al., 2020).

There are several models for the emergence of grid-patterned activity, and resonance plays distinct roles (compared to the role proposed through our analyses) in some of these models (Giocomo et al., 2007; Kropff and Treves, 2008; Burak and Fiete, 2009; Burgess and O'Keefe, 2011; Giocomo et al., 2011b; Giocomo et al., 2011a; Navratilova et al., 2012; Pastoll et al., 2012; Couey et al., 2013; Domnisoru et al., 2013; Schmidt-Hieber and Hausser, 2013; Yoon et al., 2013; Schmidt-Hieber et al., 2017; Urdapilleta et al., 2017; Stella et al., 2020; Tukker et al., 2021). However, a common caveat that spans many of these models is that they assume homogeneous networks that do not account for the ubiquitous heterogeneities that span neural circuits. Our goal in this study was to take a step towards rectifying this caveat, towards understanding the impact of neural circuit heterogeneities on network stability. We chose the 2D CAN model for grid-patterned activity generation as the substrate for addressing this important yet under-explored question on the role of biological heterogeneities on network function. As we have mentioned in the discussion section, this choice implies that our conclusions are limited to the 2D CAN model for grid patterned generation; these conclusions cannot be extrapolated to other networks or other models for grid-patterned activity generation without detailed analyses of the impact of neural circuit heterogeneities in those models. As our focus here was on the stabilizing role of resonance in heterogeneous neural networks, with 2D CAN model as the substrate, we have not implemented the other models for grid-patterned generation. The impact of biological heterogeneities and resonance on each of these models should be independently addressed with systematic analyses similar to our analyses for the 2D CAN model. As different models for grid-patterned activity generation are endowed with disparate dynamics, and have different roles for resonance, it is conceivable that the impact of biological heterogeneities and intrinsic neuronal resonance have differential impact on these different models. We have mentioned this as a clear limitation of our analyses in the discussion section, also presenting future directions for associated analyses(subsection: “Future directions and considerations in model interpretation”).

II. Brute force amputation of the low frequencies in the resonator model.

We completely agree with the reviewer on the observation that the resonator model employed in the previous version of our manuscript was rather artificial, with the realization involving brute force amputation of the lower frequencies. To address this concern, in the revised manuscript, we constructed a new mechanistic model for single-neuron resonance that matches the dynamical behavior of physiological resonators. Specifically, we noted that physiological resonance is elicited by a slow activity-dependent negative feedback (Hutcheon and Yarom, 2000). To incorporate resonance into our rate-based model neurons, we mimicked this by introducing a slow negative feedback loop into our single-neuron dynamics (the motivations are elaborated in the new results subsection “Mechanistic model of neuronal intrinsic resonance: Incorporating a slow activity-dependent negative feedback loop”). The singleneuron dynamics of mechanistic resonators were defined as follows:

Here, S governed neuronal activity, τ defined the feedback state variable, g represented the integration time constant, Ie was the external current, and g represented feedback strength. The slow kinetics of the negative feedback was controlled by the feedback time constant (τm). In order to manifest resonance, τm > τ (Hutcheon and Yarom, 2000). The steady-state feedback kernel (m∞) of the negative feedback is sigmoidally dependent on the output of the neuron (S), defined by two parameters: half-maximal activity (S1/2) and slope (k). The single-neuron dynamics are elaborated in detail in the methods section (new subsection: Mechanistic model for introducing intrinsic resonance in rate-based neurons).

We first demonstrate that the introduction of a slow-negative feedback loop introduce resonance into single-neuron dynamics (new Figure 9D–E). We performed systematic sensitivity analyses associated with the parameters of the feedback loop and characterized the dependencies of intrinsic neuronal resonance on model parameters (new Figure 9F–I). We demonstrate that the incorporation of resonance through a negative feedback loop was able to generate grid-patterned activity in the 2D CAN model employed here, with clear dependencies on model parameters (new Figure 10; new Figure 10-Supplements1–2). Next, we incorporated heterogeneities into the network and demonstrated that the introduction of resonance through a negative feedback loop stabilized grid-patterned generation in the heterogeneous 2D CAN model (new Figure 11).

The mechanistic route to introducing resonance allowed us to probe the basis for the stabilization of grid-patterned activity more thoroughly. Specifically, with physiological resonators, resonance manifests only when the feedback loop is slow (new Figure 9I; Hutcheon and Yarom, 2000). This allowed us an additional mechanistic handle to directly probe the role of resonance in stabilizing the grid patterned activity. We assessed the emergence of grid-patterned activity in heterogeneous CAN models constructed with networks constructors with neurons with different τm values (new Figure 12). Strikingly, we found that when τm value was small (resulting in fast feedback loops), there was no stabilization of gridpatterned activity in the CAN model, especially with the highest degree of heterogeneities (new Figure 12). With progressive increase in τm, the patterns stabilized with grid score increasing with τm=25 ms (new Figure 12) and beyond (new Figure 11B; τm=75 ms). Finally, our spectral analyses comparing frequency components of homogeneous vs. heterogeneous resonator networks (new Figure panels 13D–F) showed the suppression of low-frequency perturbations in heterogeneous CAN networks.

We gratefully thank the reviewer for raising the issue with the phenomenological resonator model. This allowed us to design the new resonator model and provide several new lines of evidence in support of our central hypothesis. The incorporation of resonance through a negative feedback loop also allowed us to link our analyses to the well-established role of network motifs involving negative feedback loops in inducing stability and suppressing external/internal noise in engineering and biological systems. We envisage intrinsic neuronal resonance as a cellular-scale activity-dependent negative feedback mechanism, a specific instance of a well-established network motif that effectuates stability and suppresses perturbations across different networks (Savageau, 1974; Becskei and Serrano, 2000; Thattai and van Oudenaarden, 2001; Austin et al., 2006; Dublanche et al., 2006; Raj and van Oudenaarden, 2008; Lestas et al., 2010; Cheong et al., 2011; Voliotis et al., 2014). A detailed discussion on this important link to the stabilizing role of this network motif, with appropriate references to the literature is included in the new discussion subsection “Slow negative feedback: Stability, noise suppression, and robustness”.

eLife Assessment

Antibodies that selectively bind distinct amyloid-beta variants are vital tools for Alzheimer's disease research. This valuable manuscript aims to delineate the epitope specificity in a panel of anti-amyloid-beta antibodies, including some with clinical relevance. The experiments were rigorously conducted, employing an interesting combination of established and state-of-the-art methodologies, yielding convincing findings.

Reviewer #1 (Public review):

The manuscript by Ivan et al aimed to identify epitopes on the Abeta peptide for a large set of anti-Abeta antibodies, including clinically relevant antibodies. The experimental work was well done and required a major experimental effort including peptide mutational scanning, affinity determinations, molecular dynamics simulations, IP-MS, WB and IHC. The first part of the work is focused on an assay in which peptides (15-18-mers) based on the human Abeta sequence, including some containing known PTMs, are immobilized, thus preventing aggregation and for this reason provide limited biologically-relevant information. Although some results are in agreement with previous experimental structural data (e.g. for 3D6), and some responses to disease-associated mutations were different when compared to wild-type sequences (e.g. in the case of Aducanumab) - which may have implications for personalized treatment. On the other hand, the contribution of conformation (as in oligomers and large aggregates) in antibody recognition patterns was took into consideration in the second part of the study, in which both full-length Abeta in monomeric or aggregated forms and human CSF was employed to investigate the differential epitope interaction between Aducanumab, donanemab and lecanemab. Interestingly, these results confirmed the expected preference of these antibodies for aggregated Abeta. Overall, I understand that the work is of interest to the field.

Comments on revisions:

I have no additional recommendations.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review): 

The manuscript by Ivan et al aimed to identify epitopes on the Abeta peptide for a large set of anti-Abeta antibodies, including clinically relevant antibodies. The experimental work was well done and required a major experimental effort, including peptide mutational scanning, affinity determinations, molecular dynamics simulations, IP-MS, WB, and IHC. Therefore, it is of clear interest to the field. The first part of the work is mainly based on an assay in which peptides (15-18-mers) based on the human Abeta sequence, including some containing known PTMs, are immobilized, thus preventing aggregation. Although some results are in agreement with previous experimental structural data (e.g. for 3D6), and some responses to diseaseassociated mutations were different when compared to wild-type sequences (e.g. in the case of Aducanumab) - which may have implications for personalized treatment - I have concerns about the lack of consideration of the contribution of conformation (as in small oligomers and large aggregates) in antibody recognition patterns. The second part of the study used fulllength Abeta in monomeric or aggregated forms to further investigate the differential epitope interaction between Aducanumab, Donanemab, and Lecanemab (Figures 5-7). Interestingly, these results confirmed the expected preference of these antibodies for aggregated Abeta, thus reinforcing my concerns about the conclusions drawn from the results obtained using shorter and immobilized forms of Abeta. Overall, I understand that the work is of interest to the field and should be published without the need for additional experimental data. However, I recommend a thorough revision of the structure of the manuscript in order to make it more focused on the results with the highest impact (second part).

We thank the reviewer for highlighting this critical aspect. Our rationale for beginning with the high-resolution, aggregation-independent peptide microarray was to systematically dissect sequence requirements, including PTMs, truncations, and elongations, at single–amino acid resolution. This platform defines linear epitope preferences without the confounding influence of aggregation and enabled analyses that would not have been technically feasible with fulllength Aβ. This rationale is now clarified in the Introduction (lines 72–77).

At the same time, the physiological relevance of antibody binding can only be assessed in the context of aggregation. Prompted by the reviewer’s comments, we restructured the manuscript to foreground the full-length, aggregation-dependent data (Figures 5–7). These assays demonstrate that Aducanumab preferentially recognizes aggregated peptide over monomers and that pre-adsorption with fibrils, but not monomers, blocks tissue reactivity (lines 585–599; Fig. 5B). They also show that Lecanemab can capture soluble Aβ in CSF by IP-MS (lines 544–547; Fig. 4B, Fig. 6–Supplement 1), and that Donanemab strongly binds low-molecular-weight pyroGlu-Aβ while also recognizing highly aggregated Aβ1-42 (lines 668–684; Fig. 7).

The revised Conclusion now explicitly states the complementarity of the two approaches: microarrays for precise sequence and modification mapping, and full-length aggregation assays for context and physiological relevance (lines 705–714).

Finally, prompted by the reviewer’s feedback, we refined the discussion of therapeutic antibodies to move beyond a descriptive dataset and provide mechanistic clarity. Specifically, the dimerization-supported, valency-dependent binding mode of Aducanumab and the additional structural contributions required for Lecanemab binding to aggregated Aβ are now integrated into the reworked Conclusion (lines 725–741).

Reviewer #2 (Public review):  

This paper investigates binding epitopes of different anti-Abeta antibodies. Background information on the clinical outcome of some of the antibodies in the paper, which might be important for readers to know, is lacking. There are no references to clinical outcomes from antibodies that have been in clinical trials. This paper would be much more complete if the status of the antibodies were included. The binding characteristics of aducanumab, donanemab, and Lecanemab should be compared with data from clinical phase 3 studies. 

Aducanumab was identified at Neurimmune in Switzerland and licensed to Biogen and Eisai. Aducanumab was retracted from the market due to a very high frequency of the side-effect amyloid-related imaging abnormalities-edema (ARIA-E). Gantenerumab was developed by Roche and had two failed phase 3 studies, mainly due to a high frequency of ARIA-E and low efficacy of Abeta clearance. Lecanemab was identified at Uppsala University, humanized by BioArctic, and licensed to Eisai, who performed the clinical studies. Eisai and Biogen are now marketing Lecanemab as Leqembi on the world market. Donanemab was developed by Ely Lilly and is sold in the US as Kisunla. 

We thank the reviewer for this valuable suggestion. In the revised manuscript, we have included a concise overview of the clinical status and outcomes of the therapeutic antibodies in the Introduction. This new section (lines 81–99) summarizes the origins, phase 3 trial outcomes, and current regulatory status of Aducanumab, Lecanemab, and Donanemab, as well as mentioning Gantenerumab as a comparator. Key aspects such as ARIA-E incidence, amyloid clearance efficacy, and regulatory decisions are now referenced to provide the necessary clinical context.

These additions directly link our epitope mapping data with the clinical performance and safety profiles of the antibodies, thereby making the translational implications of our results clearer for both research and therapeutic applications.

Limitations: 

(1) Conclusions are based on Abeta antigens that may not be the primary targets for some conformational antibodies like aducanumab and Lecanemab. There is an absence of binding data for soluble aggregated species.

We thank the reviewer for raising this important point. To address the absence of data on soluble aggregated species, we added IP-MS experiments using pooled human CSF as a physiologically relevant source of endogenous Aβ. Lecanemab enriched several endogenous soluble Aβ variants (Aβ1–40, Aβ1–38, Aβ1–37, Aβ1–39, and Aβ1–42), whereas Aducanumab did not yield detectable signals (Figure 4B; lines 544–547). These results directly distinguish between synthetic and patient-derived Aβ and highlight Lecanemab’s capacity to capture soluble Aβ species under biologically relevant conditions.

(2) Quality controls and characterization of different Abeta species are missing. The authors need to verify if monomers remain monomeric in the blocking studies for Figures 5 and 6. 

We thank the reviewer for this comment. In Figure 5 we show that pre-adsorption with monomeric Aβ1–42 does not prevent Aducanumab binding, whereas fibrillar Aβ1–42 completely abolishes staining, consistent with Aducanumab’s avidity-driven preference for higher-order aggregates.

For Lecanemab (Figure 6), we observed a partial preference for aggregated Aβ1–42 over HFIP-treated monomeric and low-n oligomeric forms. We note, as now stated in the revised manuscript (lines 622–623), that monomeric preparations may partially re-aggregate under blocking conditions, which represents an inherent limitation of such experiments.

To further address this, we performed additional blocking experiments using shorter Aβ peptides, which are less prone to aggregation. These peptides did not block immunohistochemical staining (Figure 6 – Supplement 1), underscoring that both epitope length and conformational state contribute to Lecanemab binding. This conclusion is also consistent with recent data presented at AAIC 2023.

(3) The authors should discuss the limitations of studying synthetic Abeta species and how aggregation might hide or reveal different epitopes. 

We thank the reviewer for this important comment. We now explicitly discuss the limitations of using synthetic Aβ peptides, including that aggregation state can mask or expose epitopes in ways that differ from endogenous species. This discussion has been added in the revised manuscript (lines 737–742).

As noted in our replies to Points (2) and (4) here, and to Reviewer #1, we addressed this experimentally by complementing the high-resolution, aggregation-independent mapping with blocking studies using aggregated and monomeric Aβ preparations, and by validating key findings with IP-MS of human CSF as a physiologically relevant source of soluble Aβ. Together, these complementary approaches mitigate the limitations of synthetic peptides and provide a more comprehensive picture of antibody–Aβ interactions

(4) The authors should elaborate on the differences between synthetic Abeta and patientderived Abeta. There is a potential for different epitopes to be available. 

We thank the reviewer for this comment. In the revised manuscript we now discuss how comparisons between synthetic and patient-derived Aβ species reveal additional, likely conformational epitopes that are not accessible in short or monomeric synthetic forms. To address this directly, we performed IP-MS with pooled human CSF. Lecanemab enriched a diverse set of endogenous soluble Aβ1–X species (Aβ1–40, Aβ1–38, Aβ1–37, Aβ1–39, and Aβ1–42), whereas Aducanumab did not yield measurable pull-down (Figure 4B; lines 544– 547). These results emphasize that patient-derived Aβ displays distinct aggregation dynamics and epitope accessibility.

We have expanded on this point in the Conclusion (lines 737–742), underscoring the

importance of integrating both synthetic and native Aβ sources to capture the full range of antibody targets. 

Reviewer #1 (Recommendations for the authors): 

This revision should prioritize the presentation of results obtained using the full-length Abeta peptide, given its more direct relevance to expected antibody recognition patterns in physiological contexts, and discuss the evidence for using synthetic Abeta. 

We thank the reviewer for this recommendation. The revised manuscript now places stronger emphasis on results obtained with full-length Aβ peptides, particularly in Figures 5–7, which analyze binding preferences across monomeric, oligomeric, and fibrillar states (lines 585–599, 609–623, 668–684). We also expanded the Discussion to outline both the rationale and the limitations of using synthetic Aβ. The microarray approach provides high-resolution, aggregation-independent sequence and modification mapping, but must be complemented by experiments with full-length Aβ1–42 under physiologically relevant conditions, such as IP-MS from CSF (lines 544–547) and blocking in IHC (lines 585–599, 622–623, 684), to capture conformational epitopes and validate functional relevance.

Figure 6. = Please review/better explain the following statement "Lecanemab recognized Aβ140, Aβ1-42, Aβ3-40, Aβ-3-40 and phosphorylated pSer8-Aβ1-40 on CIEF-immunoassay and Bicine-Tris SDS-PAGE/ Western blot, indicating that the Lecanemabbs epitope is located in the N-terminal region of the Aβ sequence". Is it possible that N-truncated peptides do not form aggregates as efficiently as (or conformationally distinct from) full-length ones? 

In the revised text we now clarify that Lecanemab recognized Aβ1-40, Aβ1-42, Aβ3-40, Aβ-340, and phosphorylated pSer8-Aβ1-40 on CIEF-immunoassay (Figure 6A; lines 612–619) and Bicine-Tris SDS-PAGE/Western blot (Figure 6C; lines 639–640). In contrast, shorter Ntruncated variants such as Aβ4-40 and Aβ5-40 did not generate detectable signals under the tested conditions. This is consistent with our initial microarray data (Figure 1), which indicated that Lecanemab binding depends on residues 3–7 of the N-terminus.

On gradient Bistris SDS-PAGE/Western blot, Lecanemab showed a partial but not exclusive preference for aggregated Aβ1-42 over monomeric or low-n oligomeric forms in the HFIPtreated preparation (Figure 6B; lines 632–633). Immunohistochemical detection of Aβ deposits in AD brain sections was efficiently blocked by pre-adsorption with monomerized, oligomeric, or fibrillar Aβ1-42 (Figure 6E; lines 643–645), but not by shorter synthetic peptides such as Aβ1-16, Aβ1-34, or Aβ1-38 (Figure 6 – Supplement 1; lines 654–663).

We also note, as now stated in the Results, that re-aggregation of HFIP-treated Aβ1-42 monomers during incubation cannot be entirely excluded (lines 622–623). Taken together, these experiments indicate that both N-terminal sequence length and conformational context are critical for Lecanemab binding, and that truncated peptides may indeed fail to reproduce the aggregate-associated conformations required for full recognition.

Reviewer #2 (Recommendations for the authors): 

Introduction: 

(1) Include examples of Lecanemab, donanemab, and gantenerumab, along with relevant references. 

We expanded the clinical-context paragraph that already covers Aducanumab, Lecanemab, and Donanemab (lines 81–96) and added Gantenerumab. 

(2) Address why gantenerumab was not included in the study. 

Due to the focus of our current study on antibodies with recently approved or late-stage clinical use (Aducanumab, Donanemab, Lecanemab), Gantenerumab was not included. 

(3) Table 1: Correct the reference for Lecanemab, should be reference 44. 

Table 1 has been updated to correct the Lecanemab reference.

(4) Line 84: Add Uppsala University and Eisai alongside Biogen for Lecanemab. 

Line 84 has been revised to acknowledge Uppsala University and Eisai alongside Biogen for the development of Lecanemab (lines 90–96).

(5) Line 539: Include the reference: "Lecanemab, Aducanumab, and Gantenerumab - Binding Profiles to Different Forms of Amyloid-Beta Might Explain Efficacy and Side Effects in Clinical Trials for Alzheimer's Disease. doi: 10.1007/s13311-022-01308-6. 

We thank the reviewer for drawing attention to this important reference (now cited as Ref. 83) provides a state-of-the-art comparison of binding profiles of Lecanemab, Aducanumab, and Gantenerumab, and we have now properly incorporated it into our manuscript. 

(6) Line 657-659: State that the findings are also applicable to Lecanemab. 

Discrepancies between analysis of the short synthetic fragments and the full-length Abeta are now resolved for Aducanumab and Lecanemab and put into context in the results section and the conclusion lines 725-740. 

(7) Figures 5 and 6: Discuss how to ensure that monomers remain monomers under the study conditions, considering the aggregation-prone nature of Abeta1-42. This aggregation could impact Lecanemab's binding to "monomers." To our knowledge, Lecanemab does not bind to monomers. The binding properties observed diverge from previously described properties for Lecanemab. Explore reasons for these discrepancies and suggest conducting complementary experiments using a solution-based assay, as per Söderberg et al, 2023. In Figure 6, note that Lecanemab is strongly avidity-driven, potentially causing densely packed monomers to expose Abeta as aggregated, affecting binding interpretation on SDS-PAGE. 

We thank the reviewer for this important point. In the revised Results and Discussion we explicitly note that HFIP-treated Aβ1–42 monomers may partially re-aggregate during incubation, which cannot be fully excluded (lines 622–623).

To complement these data, we show that Lecanemab successfully enriched soluble endogenous Aβ species (Aβ1–40, Aβ1–38, Aβ1–37, Aβ1–39, and Aβ1–42) in IP-MS from pooled CSF (lines 544–547; Fig. 4B), demonstrating its ability to bind soluble Aβ under physiologically relevant conditions.

We also now cite the Söderberg et al. (2023, PMID: 36253511) study, which reported weak but detectable binding of Lecanemab to monomeric Aβ (their Fig. 1 and Table 6). This supports our interpretation that Lecanemab is aggregation-sensitive rather than strictly aggregationdependent, in contrast to Aducanumab.

To further address sequence and conformational contributions, we performed blocking experiments with shorter, non-HFIP-treated Aβ peptides (Aβ1–16, Aβ1–34, Aβ1–38). These peptides did not block Lecanemab staining in IHC (lines 654–657; Fig. 6 – Supplement 1), indicating that both extended sequence and conformational context are necessary for recognition.

Finally, our findings are in line with preliminary data by Yamauchi et al. (AAIC 2023, DOI: 10.1002/alz.065104), who proposed that Lecanemab recognizes either a conformational epitope spanning the N-terminus and mid-region, or a structural change in the mid-region induced by the N-terminus.

eLife Assessment

This valuable work provides new insights into the role of lysine acetylation of alpha-synuclein, the protein involved in Parkinson's Disease. The evidence is mostly solid, but the claims around the potential disease relevance based on seeding assays and structural work need to be toned down, or else supported by additional experimental evidence. Overall, the work will be of interest to researchers in the fields of protein biophysics and post-translational modifications, as well as Parkinson's Disease.

Reviewer #1 (Public review):

Summary:

This paper describes experiments with alpha-synuclein (aS) with acetylated lysines (acK) at various positions. Their findings on how to use non-canonical amino acid (ncAA) mutagenesis to generate aS with acetylated lysines are valuable. The paper then continues with a range of experiments to characterise the acetylated alpha-synuclein constructs at different positions, with the aim of providing insights into which sites are relevant to disease or their function inside cells. The paper concludes these experiments with the suggestion that inhibiting the Zn2+-dependent histone deacetylase HDAC8 to potentially increase acetylation at lysine 80 may have therapeutic benefit. However, the relevance of most of these experiments is unclear, mainly as the filaments that form from these constructs are different from those observed in human disease (but see below for more details). Moreover, using the recombinantly produced acetylated versions of alpha-synuclein to normalise mass-spectrometry data, the authors themselves report that acetylation of alpha-synuclein does not differ between individuals with Parkinson's disease or healthy controls.

Strengths:

The authors report difficulties with chemical synthesis, and then decide to make these constructs using non-canonical amino acid (ncAA) mutagenesis, which seems to work reasonably well (yields vary somewhat). In the Conclusion section, the authors report that they used these recombinant proteins to obtain quantitative insights into the levels of acetylation of lysines in individuals with PD versus healthy controls, for which they find no significant differences. This part of the work is valuable.

Weaknesses:

The authors then use circular dichroism to show that aSyn with acK at position 43 has less alpha-helical content. From this result, they deduce that "only this site could potentially perturb aS function in neurotransmitter trafficking", but no experiments on neurotransmitter trafficking were performed.

Subsequently, they measure the aggregation speed of the variants in seeded aggregation experiments with preformed fibrils (PFFs) from WT aSyn, and conclude that acK at positions 12, 43, and 80 yields slower aggregation. They reach similar conclusions when measuring seeded aggregation in primary cultures. As far as I understand it, the seeding experiments in cells use seeds that are assembled from partially acetylated alpha-synuclein, but that are made of non-acetylated wildtype alpha-synuclein, and the alpha-synuclein that is endogenous in the cells is also non-acetylated (or at least not beyond what happens in these cells at endogenous levels). It is therefore unclear how the cellular seeding experiments relate to the in vitro aggregation assays with (partially) acetylated substrates. Anyway, both aggregation experiments ignore that the structures of aSyn filaments in Parkinson's disease (PD) or multiple system atrophy (MSA) are different from those formed in these experiments, and that, therefore, the observed aggregation kinetics are likely irrelevant for the speed with which disease-relevant filaments form in the brain.

NMR and FCS experiments show that acK at positions 12 and 43 may reduce binding to vesicles, which then leaves only acK80.

Finally, the authors describe the cryo-EM structure of mixtures of acK80:WT aSyn filaments, which are predominantly made of WT aSyn, with a previously described structure. Filaments made of only acK80 aSyn have a modified arrangement of this structure, where the now neutral side chain of residue 80 packs inside a hydrophobic pocket. The authors discuss differences between the acK80 structures and those of other structures from in vitro assembled aSyn filaments, none of which are the same as those observed from PD or MSA brains, nor are any attempts made to transfer observations from the in vitro experiments to the structures of disease. The relevance of the cryo-EM structures for human disease, therefore, remains unclear.

The Conclusion on p.20 mentions an interesting and valuable result: the authors used the acetylated recombinant proteins to determine the extent of acetylation within human protein samples by quantitative liquid chromatography MS (SI, Figures S41-S49). Their conclusion is that "The level of acetylation was variable - no clear trend was observed between healthy control and patients - nor between patients of different diseases (SI, Table S4, Supplementary Data 1)" This result implies that acetylation of aS is not directly related to its pathogenicity, which again adds doubts on the disease-relevance of the results described in the rest of the paper.

Reviewer #2 (Public review):

Summary:

Shimogawa et al. studied the effect of lysine acetylation at different sites in the alpha-synuclein (aS) sequence on the protein-membrane affinity, seeding capacity in the test tube and in cells, and on the structure of fibrils, using a range of biophysical methods. They use non-canonical amino acid (ncAA) mutagenesis to prepare aS lysine acetylated variant at different sites.

Strengths:

The major strength of this paper is the approach used for the production of site-specific lysine acetylated variants of aS using ncAA mutagenesis, as well as the combination of a range of biophysical methods together with cellular assays and structure biology to decipher the effect of lysine acetylation on aS-membrane binding, seeding propensity, and fibril structure. This approach allowed the author to find that lysine acetylation at positions 12, 43, and 80 led to lower seeding capacity of aS in the test tube and in cells, but only acetylation at lysine 80 did not affect aS-membrane interaction. These results suggest that lysine acetylation at position 80 may be protective against aggregation without perturbing the proposed functional role of aS in synaptic plasticity.

Weaknesses:

SDS is not a good membrane model to investigate the effect of lysine acetylation on aS membrane-binding because it is a harsh detergent and solubilizes membranes. Negatively charged vesicles or vesicles made of a mixture of lipids mimicking the lipid composition of synaptic vesicles are more accepted in the field to study aS-membrane interactions. The authors used such vesicles for the FCS experiments, and they could be used for the initial screening of the 12 lysine acetylated variants of aS.

It would help the reader to have the experimental details (e.g., buffer, protein/lipid concentrations) for the different assays written in the figure legend.

The authors use an assay consisting of mixing 10% fibrils + 90% monomer to investigate the effect of lysine acetylation on aS. However, the assay only probes fibril elongation and/or secondary processes. The current wording can be misleading, and the term aggregation could be replaced by seeding capacity for clarity. For example, the authors state that lysine acetylation at sites 12, 43, and 80 each inhibits aggregation, but this statement is not supported by the data. Instead, the data show that the acetylation at these sites slows down the fibril elongation and thus decreases the seeding capacity of aS fibrils. In order to state that lysine acetylation has an effect on aS aggregation, fibril formation, the author should use an assay where the de novo formation of fibrils is assessed, such as in the presence of lipid vesicles or under shaking conditions.

It is not clear from the EM data that the structures of the different lysine acetylated variants are different, unlike what is stated in the text.

Reviewer #3 (Public review):

Shimogawa et al. describe the generation of acetylated aSyn variants by genetic code expansion to elucidate effects on vesicle binding, aggregation, and seeding effects. The authors compared a semi-synthetic approach to obtain acetylated aSyn variants with genetic code expansion and concluded that the latter was more efficient in generating all 12 variants studied here, despite the low yields for some of them. Selected acetylated variants were used in advanced NMR, FCS, and cryo-EM experiments to elucidate structural and functional changes caused by acetylation of aSyn. Finally, site-specific differences in deacetylation by HDAC 8 were identified.

The study is of high scientific quality, andthe results are convincingly supported by the experimental data provided. The challenges the authors report regarding semi-synthetic access to aSyn are somewhat surprising, as this protein has been made by a variety of different semi-synthesis strategies in satisfactory yields and without similar problems being reported.

The role of PTMs such as acetylation in neurodegenerative diseases is of high relevance for the field, and a particular strength of this study is the use of authentic acetylated aSyn instead of acetylation-mimicking mutations. The finding that certain lysine acetylations can slow down aggregation even when present only at 10-25% of total aSyn is exciting and bears some potential for diagnostics and therapeutic intervention.

Author response:

We thank you for your efforts in reviewing our manuscript.  We sincerely appreciate that the reviewers were all enthusiastic about our comparison of native chemical ligation (NCL) and non-canonical amino acid (ncAA) mutagenesis methods for installing acetyl lysine (AcK) in alpha-synuclein, as well as the wide variety of biochemical experiments enabled by our ncAA approach.  We respond to the critiques specific to each reviewer here.

Reviewer #1:

Expressed concern that in vitro studies of effects on membrane binding were not followed up with neurotransmitter trafficking experiments.  While we certainly think that such studies would be interesting, they would presumably require the use of acetylation mimic mutants (Lys-to-Gln mutations), which we would want to validate by comparison to our semi-synthetic proteins with authentic AcK.  Such experiments are planned for a follow-up manuscript, and we will investigate the reviewer’s suggested experiment at that time.

Reviewer #1 Noted that the method of in vitro seeding really reports on the impact of acetylation on the elongation phase of aggregation.  We will clarify this in our revisions.  They also expressed concern that this was different than the role that acetylation would play in seeding cellular aggregation with pre-acetylated fibrils.  We will also acknowledge and clarify this in our revisions.  Having the monomer population acetylated in cells presents technical challenges that might also be addressed with Gln mutant mimics, and we plan to pursue such experiments in the follow-up manuscript noted above.

Reviewer #1 Criticized the fact that the pre-formed fibrils used in seeding would not have the same polymorph as PD or MSA fibrils derived from patient material.  They were also critical of how our cryo-EM structure of AcK80 fibrils related to the PD and MSA polymorphs.  Finally, while the reviewer liked the MS experiments used to quantify acetylation levels from patient samples, they felt that our findings then threw the physiological relevance of our structural and biochemical experiments into question.  We believe that all of these critiques can be addressed by clarifying our purpose.  We are not necessarily trying to claim that our AcK80 fold is populated in health or disease, but that by driving Lys80 acetylation, one could push fibrils to adopt this conformation, which is less aggregation-prone.  A similar argument has been made in investigations of alpha-synuclein glycosylation and phosphorylation.  Our results in Figure 9 imply that this could be done with HDAC8 inhibition.  We will revise the manuscript to make these ideas clearer, while being sure to acknowledge the limitations noted by Reviewer #1.

Reviewer #2:

Expressed concern over our use of SDS micelles for initial investigation of the 12 AcK variants, rather than the phospholipid vesicles used in later FCS and NMR experiments.  We will note this shortcoming in revisions of our manuscript, but we do not believe that using vesicles instead would change the conclusions of these experiments (that only AcK43 produces an effect, and a modest one at that).

We will add additional detail to the figure captions, as requested by Reviewer #2.

Reviewer #2 shared some of the concerns of Reviewer #1 regarding the distinctions of which phase of aggregation we were investigating in our in vitro experiments.  As noted above, we will clarify this language.

Finally, Reviewer #2 stated that “It is not clear from the EM data that the structures of the different lysine acetylated variants are different.”  We feel that it is quite clear from structures in Figure 8 and the EM density maps in Figure S38 that the AcK80 fold is indeed different.  Although the overall polymorphs are somewhat similar to WT, the position of K80 clearly changes upon acetylation, altering the local fold significantly and the global fold more moderately.

Reviewer #3:

Found the results convincing, including the potential therapeutic implications.  The only concern noted was that they found the difficulties in semi-synthesis of AcK-modified alpha-synuclein surprising given that it has been made many times before through NCL.  Indeed, our own laboratory has made alpha-synuclein through NCL, and the yields reported here are in keeping with our own previous results.  However, since NCL did not give higher yields than ncAA methods, and it is significantly easier to scan AcK positions using ncAAs, we felt that ncAAs are the method of choice in this case.  We will clarify this position in the revised manuscript.

In conclusion, on behalf of all authors, I again thank the reviewers for both their positive and negative observations in helping us to improve our manuscript.  We will revise it to strive for greater clarity as we have noted in this letter.

eLife Assessment

This study seeks to expand the understanding of insulin and glucose responses in the brain, specifically by implicating a family of protein kinases responsive to insulin. The significance of the study to the field is valuable, given this study is very emblematic of the new field of interoception (Brain-Body physiology). The evidence supporting the conclusions about brain glucose utilization is convincing and is relevant to many age-related diseases, such as Alzheimer's disorder.

Reviewer #1 (Public review):

Summary:

The study by Akita B. Jaykumar et al. explored an interesting and relevant hypothesis whether serine/threonine With-No-lysine (K) kinases (WNK)-1, -2, -3, and -4 engage in insulin-dependent glucose transporter-4 (GLUT4) signaling in the murine central nervous system. The authors especially focused on the hippocampus as this brain region exhibits high expression of insulin and GLUT4. Additionally, disrupted glucose metabolism in the hippocampus has been associated with anxiety disorders, while impaired WNK signaling has been linked to hypertension, learning disabilities, psychiatric disorders or Alzheimer's disease. The study took advantage of selective pan-WNK inhibitor WNK 643 as the main tool to manipulate WNK 1-4 activity both in vivo by daily, per-oral drug administration to wild-type mice, and in vitro by treating either adult murine brain synaptosomes, hippocampal slices, primary cortical cultures, and human cell lines (HEK293, SH-SY5Y). Using a battery of standard behavior paradigms such as open field test, elevated plus maze test, and fear conditioning, the authors convincingly demonstrate that the inhibition of WNK1-4 results in behavior changes, especially in enhanced learning and memory of WNK643-treated mice. To shed light on the underlying molecular mechanism, the authors implemented multiple biochemical approaches including immunoprecipitation, glucose-uptake assay, surface biotylination assay, immunoblotting, and immunofluorescence. The data suggest that simultaneous insulin stimulation and WNK1-4 inhibition results in increased glucose uptake and the activity of insulin's downstream effectors, phosphorylated Akt and phosphorylated AS160. Moreover, the authors demonstrate that insulin treatment enhances the physical interaction of the WNK effector OSR1/SPAK with Akt substrate AS160. As a result, combined treatment with insulin and the WNK643 inhibitor synergistically increases the targeting of GLUT4 to the plasma membrane. Collectively, these data strongly support the initial hypothesis that neuronal insulin- and WNK-dependent pathways do interact and engage in cognitive functions.

In response to our initial comments, the authors mildly revised the manuscript, which did not improve the weaknesses to a sufficient level. Our follow-up comments are labeled under "Revisions 1".

Strengths:

The insulin-dependent signaling in the central nervous system is relatively understudied. This explorative study delves into several interesting and clinically relevant possibilities, examining how insulin-dependent signaling and its crosstalk with WNK kinases might affect brain circuits involved in memory formation and/or anxiety. Therefore, these findings might inspire follow-up studies performed in disease models for disorders that exhibit impaired glucose metabolism, deficient memory, or anxiety, such as Diabetes mellitus, Alzheimer's disease, or most of psychiatric disorders.

The graphical presentation of the figures is of high quality, which helps the reader to obtain a good overview and to easily understand the experimental design, results, and conclusions.

The behavioral studies are well conducted and provide valuable insights into the role of WNK kinases in glucose metabolism and their effect on learning and memory. Additionally, the authors evaluate the levels of basal and induced anxiety in Figures 1 and 2, enhancing our understanding of how WNK signaling might engage in cognitive function and anxiety-like behavior, particularly in the context of altered glucose metabolism.

The data presented in Figures 3 and 4 are notably valuable and robust. The authors effectively utilize a variety of in vivo and in vitro models, combining different treatments in a clear manner. The experimental design is well-controlled, efficiently communicated, and well-executed, providing the reader with clear objectives and conclusions. Overall, these data represent particularly solid and reproducible evidence on the enhanced glucose uptake, GLUT4 targeting, and downstream effectors' activation upon insulin and WNK/OSR1 signaling crosstalk.

Weaknesses:

(1) The study used a WNK643 inhibitor as the only tool to manipulate WNK1-4 activity. This inhibitor seems selective; however, it has been reported that it exhibits different efficiency in inhibiting the individual WNK kinases among each other (e.g. PMID: 31017050, PMID: 36712947). Additionally, the authors do not analyze nor report the expression profiles or activity levels of WNK1, WNK2, WNK3, and WNK4 within the relevant brain regions (i.e. hippocampus, cortex, amygdala). Combined, these weaknesses raise concerns about the direct involvement of WNK kinases within the selected brain regions and behavior circuits. It would be beneficial if the authors provided gene profiling for WNK1, 2, 3, and -4 (e.g. using Allen brain atlas). To confirm the observations, the authors should either add results from using other WNK inhibitors or, preferentially, analyze knock-down or knock-out animals/tissue targeting the single kinases.

Revisions 1: The authors added Fig. S1A during the revisions to show expression of Wnt1-4. While the expression data from humans is interesting, the experimental part of the study is performed in mice. It would be more informative for the authors to add expression profiles from mice or overview the expression pattern with suitable references in the introduction to address this point. The authors did not add data from knock down or knockout tissue targeting the single kinases.

(2) The authors do not report any data on whether the global inhibition of WNKs affects insulin levels as such. Since the authors demonstrate the synergistic effect of simultaneous insulin treatment and WNK1-4 inhibition, such data are missing.

Revisions 1: The authors added Fig. S5A to address this point. It is appreciated that authors performed the needed experiment. Unfortunately, no significant change was found, therefore, the authors still cannot conclude that they demonstrate a synergistic effect of simultaneous insulin treatment and WNT1-4 inhibition. It is a missed opportunity that the authors did not measure insulin in the CSF or tissue lysate to support the data.

(3) The study discovered that the Sortilin receptor binds to OSR1, leading the authors to speculate that Sortilin may be involved in the insulin-dependent GLUT4 surface trafficking. The authors conclude in the result section that "WNK/OSR1/SPAK influences insulin-sensitive GLUT4 trafficking by balancing GLUT4 sequestration in the TGN via regulation of Sortilin with GLUT4 release from these vesicles upon insulin stimulation via regulation of AS160." However, the authors do not provide any evidence supporting Sortilin's involvement in such regulation, thus, this conclusion should be removed from the section. Accordingly, the first paragraph of the discussion should be also rephrased or removed.

Revisions 1: The authors added Fig. 5M-N to address this point. The new experiment is appreciated. However, the authors still do not show that sortilin is involved in insulin or WNK-dependent GLUT4 trafficking in their set up since the authors do not demonstrate any changes in GLUT4 sorting or binding. The conclusions should therefore be rephrased or included purely in the discussion. Moreover, the discussion was not adjusted either, leading to over interpretation based on the available data.

(4) The background relevant to Figure 5, as well as the results and conclusions presented in Figure 5 are quite challenging to follow due to the lack of a clear introduction to the signaling pathways. Consequently, understanding the conclusions drawn from the data is also difficult. It would be beneficial if the authors addressed this issue with either reformulations or additional sections in the introduction. Furthermore, the pulldown experiments in this figure lack some of the necessary controls.

Revisions 1: The Authors insufficiently addressed this point during the revisions and did not rewrite the introduction as suggested.

(5) The authors lack proper independent loading controls (e.g. GAPDH levels) in their immunoblots throughout the paper, and thus their quantifications lack this important normalization step. The authors also did not add knock-out or knock-down controls in their co-IPs. This is disappointing since these improvements were central and suggested during the revision process.

(6) The schemes that represent only hypotheses (Fig. 1K, 4A) are unnecessary and confusing and thus should be omitted or placed at the end of each figure if the conclusions align.

(7) Low-quality images, such as Fig. 5H should be replaced with high-resolution photos, moved to the supplementary, or omitted.

Reviewer #2 (Public review):

This study by Jaykumar and colleagues seeks to expand the field's appreciation of insulin responses in the brain, specifically by implicating WNK kinase function in various neuronal responses, ranging from behavioral / memory changes to GLUT4 trafficking to the cell surface with subsequent glucose uptake. This revised study is now comprehensive and presents a logical and reasonably documented cascade of molecular interactions responsible in part for GLUT4 trafficking under the regulation of WKK and insulin. Additional data allow the authors to dissect a plausible WNK/OSR1/SPAK-sortilin pathway for the modulation of GLUT4 trafficking, in part by capitalizing on a overlay of various techniques and systems. The data - much of it in vivo or ex vivo - showing a potential role for WNK function in brain glucose utilization remains a compelling part of the story, with the dissection of the signaling cascade and a potential role for sortilin in mediating WNK function via effects on GLUT4 cellular localization now more convincing.

Initially, the group shows that oral WNK463 treatment - an inhibitor of WNKs broadly - in mice augments a number of memory readouts. These findings fit within the context of the overall story the authors present: that WNK function is critical to brain glucose utilization, which impacts learning. Multiple approaches are used to show that WNK463 treatment, i.e. inhibition of WNKs, increases glucose uptake, including labeled 2-deoxyglucose uptake in vivo in the brain and in isolated synaptosome, and uptake in ex vivo hippocampal slices. These findings are solid and consistent. With the exception of some relatively minor comments regarding the data presentation made to the authors and now fully addressed, the findings showing that WNK463 treatment increases GLUT4-mediated glucose uptake and surface localization of GLUT4 are reasonable, with the hippocampal slice data being particularly relevant.

While the details of the WNK signaling cascade is dense, in the revised application one clearly appreciates the molecular interrogation and interactions the group is dissecting, supported by the use of multiple models. With the additional findings, these systems and the data now reinforce each other, presenting a strongly documented overall story.

A limitation of the study with the initial submission was the authors' reliance upon a single pharmacological tool (WNK463) to inhibit WNK kinases. WNK463 apparently has substantial specificity for WNKs and WNK463 treatment lessened OSR1 phosphorylation (a WNK substrate). Nevertheless, the cohesiveness of the findings in terms of the broader pathway engagement (GLUT4 trafficking, glucose uptake) is consistent with the author's proposed mechanisms and conclusions. The authors have additionally addressed this concern in the revised manuscript with more information supporting the specificity of WNK463 as well as the multiple approaches to confirm the effect of WNK463 on the WNK signaling pathway of interest.

The final few paragraphs of the discussion that weave the author's findings into the field more broadly, including Sortilin function and neurological disorders, are appreciated. Additional clarity in the Methods section is also helpful.

Author response:

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

Joint Public Review:

Summary:

The major issues are the need for more information concerning WNK expression in brain regions and additional confirmation of the role of sortilin on WNT signaling. There is a lack of sufficient evidence supporting sortilin's involvement in insulin- and WNK-dependent GLUT4 regulation. The recommendation is to examine what WNK kinase is selectively expressed in the region of interest and then explore its engagement with the sortilin and GLUT4 pathways. Further identification of components of the WNK/OSr1/SPAK-sortilin pathway that regulate GLUT4 in brain slices or primary neurons will be helpful in confirming the results. The use of knock-down or knock-out models would be helpful to explore the direct interaction of the pathways. Immortalized and primary cells also represent useful models.

Together our results indicate that one or more WNK family members regulate insulin sensitivity.  As all WNK family members are expressed in relevant brain regions, whether the results are due to actions of a single WNK family member or more likely due to their combined impact will be an important question to ask in the future.  

There are multiple publications describing how sortilin is involved in insulin-dependent Glut4 trafficking; thus, we did not further address that issue.  We have added data on an additional action of WNK463 which indicates that it can block association of OSR1 with sortilin.  While these results do not delve further into how sortilin works, they support the conclusion that WNK/OSR1/SPAK can influence insulin-dependent glucose transport via distinct cellular events (AS160, sortilin, Akt) which are WNK463 sensitive.  

Altogether we added 12 new panels of data from new and previously performed experiments and we modified 3 existing subfigures in response to comments.

Weaknesses:

(1) The study used a WNK643 inhibitor as the only tool to manipulate WNK1-4 activity. This inhibitor seems selective; however, it has been reported that it exhibits different efficiency in inhibiting the individual WNK kinases among each other (e.g. PMID: 31017050, PMID: 36712947). Additionally, the authors do not analyze nor report the expression profiles or activity levels of WNK1, WNK2, WNK3, and WNK4 within the relevant brain regions (i.e. hippocampus, cortex, amygdala). Combined, these weaknesses raise concerns about the direct involvement of WNK kinases within the selected brain regions and behavior circuits. It would be beneficial if the authors provided gene profiling for WNK1, 2, 3, and -4 (e.g. using Allen brain atlas). To confirm the observations, the authors should either add results from using other WNK inhibitors or, preferentially, analyze knock-down or knock-out animals/tissue targeting the single kinases.

Thank you for the excellent suggestion to include mRNA data for the four WNKs. We have included a supplementary figure showing expression of WNK1-4 mRNAs in prefrontal cortex and the hippocampus curated from the Allen Brain Atlas. As per the Allen Brain Atlas, all four WNKs are detected in these regions with WNK4 mRNA the most highly expressed followed by WNK2, WNK3 and then WNK1 (Figure S1A).   

With regard to the use of WNK463, we continue to use WNK463 because we have examined its actions in cell lines that only express WNK1, e.g. A549 (Haman Center lung cancer RNA-seq data), and in A549 with WNK1 deleted using CRISPR in which we saw no effects of WNK463 on several assays we use for WNK1 including suppression of autophagy.  WNK463 was reported in the literature to inhibit only the four WNKs out of more than 400 kinases tested, indicating more selectivity than many small molecules used to target other enzymes.  In other cell lines, we also use WNK1 knockdown which replicates the effect of WNK463 (Figure S7A-D). However, in SHSY5Y cells, WNK1 knockdown did not replicate the effect of WNK463 on pAKT levels (Figure S7E-F), suggesting a cooperativity among other WNK family members in neuronal cells. This makes WNK463 an ideal tool to test our hypotheses in this study as it targets all 4 WNKs (WNK1-4).  

(2) The authors do not report any data on whether the global inhibition of WNKs affects insulin levels. Since the authors wish to demonstrate the synergistic effect of simultaneous insulin treatment and WNK1-4 inhibition, such data are missing.

Thank you for this comment. To obtain this information, we treated C57BL/6J mice with WNK463 for 3 days once daily at a dose of 6 mg/kg and then fasted overnight. Plasma insulin levels were measured. Results showed that the plasma insulin levels trended upwards in the WNK463 treated animals compared to the vehicle treated groups but failed to reach any statistical significance. We have now included these data in supplementary figure S5A.

The study discovered that the Sortilin receptor binds to OSR1, leading the authors to speculate that Sortilin may be involved in the insulin-dependent GLUT4 surface trafficking. However, the authors do not provide any evidence supporting Sortilin's involvement in insulin- or WNKdependent GLUT4 trafficking. Thus, this conclusion should be qualified, rephrased, or additional data included.

Work from several groups have shown that sortilin is involved in insulin-dependent GLUT4 trafficking, for example [9-11,135-139] as we noted in the manuscript. We now show that WNK463 blocks co-immunoprecipitation of Flag-tagged sortilin with endogenous OSR1 in HEK293T cells. This result supports our model for WNK/OSR1/SPAK- insulin mediated regulation of sortilin.  We included these data in figures 5M, 5N.

Minor issues:

(1) The method and result sections lack information regarding the gender and age of mice used in the behavioral experiments. This information should be added.

Thank you for pointing this out. We apologize for the omission. The requested information has now been added in the methods section.

(2) The authors present an analysis of relative protein levels in Figure 1B and Figure 4B, however, the original immunoblots (?) are not included in the study. These data should be added to provide complete and transparent evidence for the analysis.

Thank you for this request. The blots have now been included in the supplementary figure S2A and Figure 4B, respectively.  

(3) The basis for Figure 3A needs to be explained and supported with suitable references either in the background or in the result section.

Thank you for pointing this out. Figure 3A has been moved to Figure 3H as it represents the model summary of the data presented in Figure 3. Other figure numbers have been changed accordingly.  This figure 3A (now 3H) and the model diagram of Figure 5 (now Figure 5O) are now cited in the Discussion, where the results are considered in detail.      

(4) Figure 4E should be labeled as 'Primary cortical neurons' for clarity, as the major focus is on the hippocampus. To increase consistency, the authors should consider performing the same experiment on hippocampal cultures or explaining using cortical neurons.

Thank you for the suggestion. Figure 4E (now 4F) has been labelled as Primary cortical neurons for clarity. The major focus of this study is to understand the regulation of WNKmediated regulation of insulin signaling in the areas of the brain that are insulin sensitive such as the hippocampus and the prefrontal cortex. Therefore, we included cortical neurons to test this hypothesis.  

(5) Figure 5B: The use of whole brain extracts is inconsistent with the rest of the study, especially considering the indication of differing insulin activity in selected brain regions. The authors should explain why they could not use only hippocampal tissue.

In this manuscript, we are trying to test our hypothesis in insulin-sensitive neuronal cells which includes, but not limited to, the hippocampus. Figure 5B used whole brain extracts, which contain brain regions that are insulin-sensitive as well as insulin-insensitive regions, to show the association between OSR1 and AS160. However, this observation was replicated in the insulin-sensitive SH-SY5Y cell model suggesting that association of OSR1 and AS160 is modulated in the presence of insulin as shown in Figure 5B, 5C. We added data from SH-SY5Y cells showing effects of WNK463. These data support the concept that this is an interaction that is modulated by WNKs and will occur as long as both OSR1/SPAK and AS160 are expressed.

(6) Figure 5B-C - Knock-out or knock-down condition should be included in the co-IP experiment. This is especially straightforward to generate in the SH-SY5Y cells. Moreover, these figures lack loading controls.

If we understand correctly, the issue with regard to including knockdown conditions stems from the issues raised regarding specificity of the antibody which we have addressed in point 10 below. We have now included input blots for both AS160 and OSR1 which serve as the loading control for the IP experiment in figure 5B and 5C.

(7) Figure 5C-D - A condition with WNK463 inhibition alone is missing. This condition is necessary for evaluating the effects of WNK643 inhibition with and without insulin stimulation.

Thank you for this observation. We have now added the data for that condition.  The aim of this experiment in Figure 5C (now 5B and 5C) is to show that insulin is important to facilitate interaction between OSR1 and AS160 in differentiated SHSY5Y cells and the effect of WNK463 to diminish this insulin-dependent interaction. With only WNK463, there was minimal interaction between AS160 and OSR1 as now shown in Figure 5B, 5C.

(8) Figure 5G - This figure shows the overexpression of plasmids in HEK cells, however, it lacks samples that overexpress the plasmid individually (single expression). Such data should be added, especially when the addition of the blocking peptide does not fully disable the interaction between AS160 and SPAK. Additionally, this figure also lacks a loading control, which is essential for validating the results.

Thank you for this comment. Figure 5G (now Figure 5F, 5G) is an in vitro IP in which we have mixed a purified Flag-SPAK fragment residues 50-545 with a lysate from cells expressing Myc-AS160 (residues 193-446). This is essentially an in vitro IP; because it is not an IP experiment from cell lysates where we overexpressed these plasmids which would require a loading control. The lysates were divided in half and one half did not receive the blocking peptide while the other half did, creating a control. From our experience, this blocking peptide does not completely block interactions between SPAK/OSR1 and NKCC2 fragments which are well-characterized interacting partners [a]. The reason for the partial block in interactions could also be attributed to the multivalent nature of interaction between these proteins. This confusion in our methodology used has been noted and we have tried to explain it with more clarity in the methods, results and the figure legend section. Our Commun. Biol. paper [134] that describes this assay and uses it extensively is now available online.

(a) Piechotta K, Lu J, Delpire E. Cation chloride cotransporters interact with the stressrelated kinases Ste20-related proline-alanine-rich kinase (SPAK) and oxidative stress response 1 (OSR1) J Biol Chem. 2002;277:50812–50819. doi: 10.1074/jbc.M208108200.

(9) Figure 5J, L - These figures are missing negative controls. The authors should add Sortilin knock-down or knock-out conditions for the immunoprecipitation experiments. Also, the figures lack loading controls. Moreover, the labeling "Control" should be specified, as it is unclear what this condition represents.

Thank you for noting the lack of clarity in the controls provided. Controls in Figure 5J and 5L refer to IgG Control which serves as the negative control in this case. This has now been specified in the figures (and added Figures 5M and 5N, as well). The issue with OSR1 and sortilin antibody specificity and cross-reaction has been addressed in point 10.

(10) Figure 5I - The fluorescent signals for the individual channels of OSR1 and Sortilin appear identical (even within the background signal). This raises concerns about potential antibody cross-reaction. One potential solution would be to include additional stainings with different antibodies and perform staining of each protein alone to ensure the specificity of the colocalization.

Thank you for pointing this out and giving us an opportunity to provide better images that will address the issues raised regarding antibody cross-reaction and antibody specificity. We realize that the images that we originally provided appeared to show all the puncta colocalize which could give rise to the concern about potential antibody cross-reaction. We have replaced them with more appropriate representative images that clearly show some selected regions of common staining as well as regions where there is no overlap.  

(11) Figures 5D, 5F, 5H, 5L, 5M: These analyses should be first normalized to the loading control such as GAPDH.

In Figure 5F (now 5E), the analysis has been normalized to the total AS160 protein levels. Because we are reporting changes in pAS160 protein, normalizing it to the total AS160 gives a better idea about the changes in the phosphorylated AS160 form compared to the whole protein and this is more appropriate compared to other loading controls such as GAPDH.  

In Figure 5H (now Figure 5G), the analysis is an in vitro IP assay using purified protein fragments. Therefore, using GAPDH as a control is not applicable in this case. Please refer to our response to comment 8 for details.

In Figures 5L, 5M and 5D (now 5K, 5L, 5C) shown, the IP proteins have been normalized to the input protein levels serving as a loading control for the IP experiment. 

(12) Figure 5K: The significance/meaning of the red star is unclear. It should be explained in the figure legend.

Thank you for the opportunity to enhance the readability of our manuscript. The meaning of red star denotes the condition in the yeast two-hybrid assay which shows the binding of CCT of OSR1 with C-terminus of sortilin. This has now been clarified in the figure legend.

(13) Differences in WNK643 dosage and administration periods can affect the results. There is a lack of explanation with regard to the divergent WNK643 treatments of mice across different behavior conditions of fear conditioning, the novel object test, and the elevated plus maze test. This should be considered.

Thank you for pointing out that the explanation regarding the WNK463 dosage and times are unclear. WNK463 was dosed 3 days before the start of the behavior experiment daily at a dose of 6 mg/kg and continued throughout the test protocol. This is the same protocol used for all experiments.  The text describing the protocol has been reworded with more clarity on dosage and times in methods and result section.

eLife Assessment

This study provides valuable data on the role of Hsd17b7, a gene involved in cholesterol biosynthesis, as a potential regulator of mechanosensory hair cell function. The authors used both zebrafish and the HEI cell line to examine the effects of deletion of Hsd17b7 on hair cell function and survival. While the results do show a reduction in hair cells in the lateral line neuromasts of Hsd17b7 mutant fish, the reduction was limited. The findings are considered incomplete, with additional experiments required to confirm the conclusions.

Reviewer #1 (Public review):

Summary:

This study identifies HSD17B7 as a cholesterol biosynthesis gene enriched in sensory hair cells, with demonstrated importance for auditory behavior and potential involvement in mechanotransduction. Using zebrafish knockdown and rescue experiments, the authors show that loss of hsd17b7 reduces cholesterol levels and impairs hearing behavior. They also report a heterozygous nonsense variant in a patient with hearing loss. The gene mutation has a complex and somewhat inconsistent phenotype, appearing to mislocalize, reduce mRNA and protein levels, and alter cholesterol distribution, supporting HSD17B7 as a potential deafness gene.

While the study presents an interesting candidate and highlights an underexplored role for cholesterol in hair cell function, several important claims are insufficiently supported, and the mechanistic interpretations remain somewhat murky.

Strengths:

(1) HSD17B7 is a new candidate deafness gene with plausible biological relevance.

(2) Cross-species RNAseq convincingly shows hair-cell enrichment.

(3) Lipid metabolism, particularly cholesterol homeostasis, is an emerging area of interest in auditory function.

(4) The connection between cholesterol levels and MET is potentially impactful and, if substantiated, would represent a significant advance.

Weaknesses:

(1) The pathogenic mechanism of the E182STOP variant is unclear: The mutant protein presumably does not affect WT protein localization, arguing against a dominant-negative effect. Yet, overexpression of HSD17B7-E182* alone causes toxicity in zebrafish, and it binds and mislocalizes cholesterol in HEI-OC1 cells, suggesting some gain-of-function or toxic effect. In addition, the mRNA of the variant has a low expression level, suggesting nonsense-mediated decay. This complexity and inconsistency need clearer explanation.

(2) The link to human deafness is based on a single heterozygous patient with no syndromic features. Given that nearly all known cholesterol metabolism disorders are syndromic, this raises concerns about causality or specificity. The term "novel deafness gene" is premature without additional cases or segregation data.

(3) The localization of HSD17B7 should be clarified better: In HEI-OC1 cells, HSD17B7 localizes to the ER, as expected. In mouse hair cells, the staining pattern is cytosolic and almost perfectly overlaps with the hair cell marker used, Myo7a. This needs to be discussed. Without KO tissue, HSD17B7 antibody specificity remains uncertain.

Reviewer #2 (Public review):

A summary of what the authors were trying to achieve.

The authors aim to determine whether the gene Hsb17b7 is essential for hair cell function and, if so, to elucidate the underlying mechanism, specifically the HSB17B7 metabolic role in cholesterol biogenesis. They use animal, tissue, or data from zebrafish, mouse, and human patients.

Strengths:

(1) This is the first study of Hsb17b7 in the zebrafish (a previous report identified this gene as a hair cell marker in the mouse utricle).

(2) The authors demonstrate that Hsb17b7 is expressed in hair cells of zebrafish and the mouse cochlea.

(3) In zebrafish larvae, a likely KO of the Hsb17b7 gene causes a mild phenotype in an acoustic/vibrational assay, which also involves a motor response.

(4) In zebrafish larvae, a likely KO of the Hsb17b7 gene causes a mild reduction in lateral line neuromast hair cell number and a mild decrease in the overall mechanotransduction activity of hair cells, assayed with a fluorescent dye entering the mechanotransduction channels.

(5) When HSB17B7 is overexpressed in a cell line, it goes to the ER, and an increase in Cholesterol cytoplasmic puncta is detected. Instead, when a truncated version of HSB17B7 is overexpressed, HSB17B7 forms aggregates that co-localize with cholesterol.

(6) It seems that the level of cholesterol in crista and neuromast hair cells decreases when Hsb17b7 is defective (but see comment below).

Weakness:

(1) The statement that HSD17B7 is "highly" expressed in sensory hair cells in mice and zebrafish seems incorrect for zebrafish:

(a) The data do not support the notion that HSB17B7 is "highly expressed" in zebrafish. Compared to other genes (TMC1, TMIE, and others), the HSB17B7 level of expression in neuromast hair cells is low (Figure 1F), and by extension (Figure 1C), also in all hair cells. This interpretation is in line with the weak detection of an mRNA signal by ISH (Figure 1G I"). On this note, the staining reported in I" does not seem to label the cytoplasm of neuromast hair cells. An antisense probe control, along with a positive control (such as TMC1 or another), is necessary to interpret the ISH signal in the neuromast.

(b) However, this is correct for mouse cochlear hair cells, based on single-cell RNA-seq published databases and immunostaining performed in the study. However, the specificity of the anti-HSD17B7 antibody used in the study (in immunostaining and western blot) is not demonstrated. Additionally, it stains some supporting cells or nerve terminals. Was that expression expected?

(2) A previous report showed that HSD17B7 is expressed in mouse vestibular hair cells by single-cell RNAseq and immunostaining in mice, but it is not cited:

Spatiotemporal dynamics of inner ear sensory and non-sensory cells revealed by single-cell transcriptomics.

Jan TA, Eltawil Y, Ling AH, Chen L, Ellwanger DC, Heller S, Cheng AG.

Cell Rep. 2021 Jul 13;36(2):109358. doi: 10.1016/j.celrep.2021.109358.

(3) Overexpressed HSD17B7-EGFP C-terminal fusion in zebrafish hair cells shows a punctiform signal in the soma but apparently does not stain the hair bundles. One limitation is the consequence of the C-terminal EGFP fusion to HSD17B7 on its function, which is not discussed.

(4) A mutant Zebrafish CRISPR was generated, leading to a truncation after the first 96 aa out of the 340 aa total. It is unclear why the gene editing was not done closer to the ATG. This allele may conserve some function, which is not discussed.

(5) The hsd17b7 mutant allele has a slightly reduced number of genetically labeled hair cells (quantified as a 16% reduction, estimated at 1-2 HC of the 9 HC present per neuromast). On a note, it is unclear what criteria were used to select HC in the picture. Some Brn3C:mGFP positive cells are apparently not included in the quantifications (Figure 2F, Figure 5A).

(6) The authors used FM4-64 staining to evaluate the hair cell mechanotransduction activity indirectly. They found a 40% reduction in labeling intensity in the HCs of the lateral line neuromast. Because the reduction of hair cell number (16%) is inferior to the reduction of FM4-64 staining, the authors argue that it indicates that the defect is primarily affecting the mechanotransduction function rather than the number of HCs. This argument is insufficient. Indeed, a scenario could be that some HC cells died and have been eliminated, while others are also engaged in this path and no longer perform the MET function. The numbers would then match. If single-cell staining can be resolved, one could determine the FM4-64 intensity per cell. It would also be informative to evaluate the potential occurrence of cell death in this mutant. On another note, the current quantification of the FM4-64 fluorescence intensity and its normalization are not described in the methods. More importantly, an independent and more direct experimental assay is needed to confirm this point. For example, using a GCaMP6-T2A-RFP allele for Ca2+ imaging and signal normalization.

(7) The authors used an acoustic startle response to elicit a behavioral response from the larvae and evaluate the "auditory response". They found a significative decrease in the response (movement trajectory, swimming velocity, distance) in the hsd17b7 mutant. The authors conclude that this gene is crucial for the "auditory function in zebrafish".

This is an overstatement:

(a) First, this test is adequate as a screening tool to identify animals that have lost completely the behavioral response to this acoustic and vibrational stimulation, which also involves a motor response. However, additional tests are required to confirm an auditory origin of the defect, such as Auditory Evoked Potential recordings, or for the vestibular function, the Vestibulo-Ocular Reflex.

(b) Secondly, the behavioral defects observed in the mutant compared to the control are significantly different, but the differences are slight, contained within the Standard Deviation (20% for velocity, 25% for distance). To this point, the Figure 2 B and C plots are misleading because their y-axis do not start at 0.

(8) Overexpression of HSD17B7 in cell line HEI-OC1 apparently "significantly increases" the intensity of cholesterol-related signal using a genetically encoded fluorescent sensor (D4H-mCherry). However, the description of this quantification (per cell or per surface area) and the normalization of the fluorescent signal are not provided.

(9) When this experiment is conducted in vivo in zebrafish, a reduction in the "DH4 relative intensity" is detected (same issue with the absence of a detailed method description). However, as the difference is smaller than the standard deviation, this raises questions about the biological relevance of this result.

(10) The authors identified a deaf child as a carrier of a nonsense mutation in HSB17B7, which is predicted to terminate the HSB17B7 protein before the transmembrane domain. However, as no genetic linkage is possible, the causality is not demonstrated.

(11) Previous results obtained from mouse HSD17B7-KO (citation below) are not described in sufficient detail. This is critical because, in this paper, the mouse loss-of-function of HSD17B7 is embryonically lethal, whereas no apparent phenotype was reported in heterozygotes, which are viable and fertile. Therefore, it seems unlikely that heterozygous mice exhibit hearing loss or vestibular defects; however, it would be essential to verify this to support the notion that the truncated allele found in one patient is causal.

Hydroxysteroid (17beta) dehydrogenase 7 activity is essential for fetal de novo cholesterol synthesis and for neuroectodermal survival and cardiovascular differentiation in early mouse embryos.

Jokela H, Rantakari P, Lamminen T, Strauss L, Ola R, Mutka AL, Gylling H, Miettinen T, Pakarinen P, Sainio K, Poutanen M.<br /> Endocrinology. 2010 Apr;151(4):1884-92. doi: 10.1210/en.2009-0928. Epub 2010 Feb 25.

(12) The authors used this truncated protein in their startle response and FM4-64 assays. First, they show that contrary to the WT version, this truncated form cannot rescue their phenotypes when overexpressed. Secondly, they tested whether this truncated protein could recapitulate the startle reflex and FM4-64 phenotypes of the mutant allele. At the homozygous level (not mentioned by the way), it can apparently do so to a lesser degree than the previous mutant. Again, the differences are within the Standard Deviation of the averages. The authors conclude that this mutation found in humans has a "negative effect" on hearing, which is again not supported by the data.

(13) The authors looked at the distribution of the HSB17B7 in a cell line. The WT version goes to the ER, while the truncated one forms aggregates. An interesting experiment consisted of co-expressing both constructs (Figure S6) to see whether the truncated version would mislocalize the WT version, which could be a mechanism for a dominant phenotype. However, this is not the case.

(14) Through mass spectrometry of HSB17B7 proteins in the cell line, they identified a protein involved in ER retention, RER1. By biochemistry and in a cell line, they show that truncated HSB17B7 prevents the interaction with RER1, which would explain the subcellular localization.

Hydroxysteroid (17beta) dehydrogenase 7 activity is essential for fetal de novo cholesterol synthesis and for neuroectodermal survival and cardiovascular differentiation in early mouse embryos.

Jokela H, Rantakari P, Lamminen T, Strauss L, Ola R, Mutka AL, Gylling H, Miettinen T, Pakarinen P, Sainio K, Poutanen M.<br /> Endocrinology. 2010 Apr;151(4):1884-92. doi: 10.1210/en.2009-0928. Epub 2010 Feb 25.

(15) Information and specificity validation of the HSB17B7 antibody are not presented. It seems that it is the same used on mice by IF and on zebrafish by Western. If so, the antibody could be used on zebrafish by IF to localize the endogenous protein (not overexpression as done here). Secondly, the specificity of the antibody should be verified on the mutant allele. That would bring confidence that the staining on the mouse is likely specific.

eLife Assessment

Zebra finches are a prominent model system for vocal learning and auditory system function, yet little is known about the functional development of the auditory system. Here, the authors convincingly show that newly hatched zebra finches lack detectable auditory brainstem responses and that auditory neural signals emerge only days after hatching, challenging influential claims of prenatal acoustic communication in altricial birds. This important work clarifies the developmental timeline for auditory communication and highlights the value of neuroscientific methods for validating and complementing behavioral ecological studies of animal perception.

Reviewer #1 (Public review):

This work by Antonnen et al. was triggered by claims of auditory-mediated effects on altricial avian embryos, which were published without any direct evidence that the relevant parental vocalizations were actually heard. I agree with Anttonen et al. that, based on the available evidence about avian auditory development, those claims are highly speculative and therefore necessitate more direct experimental verification.

Attonen et al. have embarked on a comprehensive series of experiments to:

(1) Better characterize acoustically the relevant parental vocalizations (heat whistles; in a separate preprint, not reviewed here)

(2) Characterize the auditory sensitivity of zebra finches at various stages of their posthatching development. Despite the long-standing importance of the zebra finch as a songbird model in neuroethology of learned vocalizations, the auditory development of the species has not been studied so far.

(3) Explore an alternative hypothesis of how the parental vocalizations might be perceived.

The principal method used here is the non-invasive recording of ABR (auditory brainstem response), a standard neurophysiological method in auditory research. The click-evoked ABR provides a quick and objective assessment of basic hearing sensitivity that does not require animal training. Weaknesses of the technique include its limited frequency specificity and low signal-to-noise ratio. The authors are experienced with ABR measurements and well aware of those issues. ABR responses in zebra finches are shown to gradually appear during the first week posthatching and to mature in subsequent weeks, consistent with the auditory development in other altricial bird species studied previously. When matching the acoustic properties of parental heat whistles and auditory sensitivities, hearing of the parental heat whistles by zebra finch hatchlings was convincingly excluded. Although not directly measured, this also convincingly extrapolates to zebra finch embryos. Finally, the authors tested the hypothesis that parental heat whistles could induce perceptible vibrations of the egg and thus stimulate the embryo via a different modality. The method used here was laser doppler vibrometry, an appropriate, state-of-the-art technique that the authors also have proven experience with. The induced vibrations were shown to be several orders of magnitude below known vibrotactile sensitivities in mammals and birds. Thus, although zebra finch vibrotactile thresholds were not obtained directly, the hypothesis of vibrotactile perception of parental heat whistles by zebra finch embryos could also be rejected convincingly.

In summary, even when considering some weaknesses of the techniques (which the authors are aware of), the conclusions of the paper are well supported: Auditory and/or vibration perception of parental heat whistles can be excluded as an explanation for previous reports of developmental programming for high ambient temperatures. As a constructive suggestion towards resolving the apparent paradox, the authors recommend repeating some of the crucial, previous playback experiments at lower sound levels that better match the natural parental vocalizations.

Reviewer #2 (Public review):

This study by Anttonen, Christensen-Dalsgaard, and Elemans describes the development of hearing thresholds in an altricial songbird species, the zebra finch. The results are very clear and along what might have been expected for altricial birds: at hatch (2 days post-hatch), the chicks are functionally deaf. Auditory evoked activity in the form of auditory brainstem responses (ABR) can start to be detected at 4 days post-hatch, but only at very loud sound levels. The study also shows that ABR response matures rapidly and reaches adult-like properties around 25 days post-hatch. The functional development of the auditory system is also frequency dependent, with a low-to-high frequency time course. All experiments are very well performed. The careful study throughout development and with the use of multiple time-points early in development is important to further ensure that the negative results found right after hatching are not the result of the experimental manipulation. The results themselves could be classified as somewhat descriptive, but, as the authors point out, they are particularly relevant and timely. Since 2016, there have been a series of studies published in high-profile journals that have presumably shown the importance of prenatal acoustic communication in altricial birds, mostly in zebra finches. This early acoustic communication would serve various adaptive functions. Although acoustic communication between embryos in the egg and parents has been shown in precocial birds (and crocodiles), finding an important function for prenatal communication in altricial birds came as a surprise. Unfortunately, none of those studies performed a careful assessment of the chicks' hearing abilities. This is done here, and the results are clear: zebra finches at 2 and 6 days post-hatch are functionally deaf. Since it is highly improbable that the hearing in the egg is more developed than at birth, one can only conclude that zebra finches in the egg (or at birth) cannot hear the heat whistles. The paper also ruled out the detection on egg vibrations as an alternative path. The prior literature will have to be corrected, or further studies conducted to solve the discrepancies. For this purpose, the "companion" paper on bioRxiv that studies the bioacoustical properties of heat calls from the same group will be particularly useful. Researchers from different groups will be able to precisely compare their stimuli.

Beyond the quality of the experiments, I also found that the paper was very well written. The introduction was particularly clear and complete (yet concise).

Weaknesses:

My only minor criticism is that the authors do not discuss potential differences between behavioral audiograms and ABRs. Optimally, one would need to repeat the work of Okanoya and Dooling with your setup and using the same calibration. The ~20dB difference might be real, or it might be due to SPL measured with different instruments, at different distances, etc. Either way, you could add a sentence in the discussion that states that even with the 20 dB difference in audiogram heat whistles would not be detected during the early days post-hatch. But adding a (novel) behavioral assay in young birds could further resolve the issue.

More Minor Points:

(1) As mentioned in the main text, the duration of pips (from pips to bursts) affects the effective bandwidth of the stimulus. I believe that the authors could give an estimate of this effective bandwidth, given what is known from bird auditory filters. I think that this estimate could be useful to compare to the effective bandwidth of the heat-call, which can now also be estimated.

(2) Figure 5b. Label the green and pink areas as song and heat-call spectrum. Also note that in the legend the authors say: "Green and red areas display the frequency windows related to the best hearing sensitivity of zebra finches and to heat calls, respectively". I don't think this is what they meant. I agree that 1-4 kHz is the best frequency sensitivity of zebra finches, but they probably meant green == "song frequency spectrum" and pink == "heat call spectrum". In either case, the figure and the legend need clarification.

(3) Figure 5c. Here also, I would change the song and heat-call labels to "song spectrum", "heat call spectrum". The authors would not want readers to think that they used song and heat calls in these experiments (maybe next time?). For the same reason, maybe in 5a you could add a cartoon of the oscillogram of a frequency sweep next to your speaker.

(4) Methods. In the description of the stimulus, the authors describe "5ms long tone bursts", but these are the tone pips in the main part of the manuscript. Use the same terms.

Reviewer #3 (Public review):

Summary

Following recent findings that exposure to natural sounds and anthropogenic noise before hatching affects development and fitness in an altricial songbird, this study attempts to estimate the hearing capacities of zebra finch nestlings and the perception of high frequencies in that species. It also tries to estimate whether airborne sound can make zebra finch eggs vibrate, although this is not relevant to the question.

Strength

That prenatal sounds can affect the development of altricial birds clearly challenges the long-held assumption that altricial avian embryos cannot hear. However, there is currently no data to support that expectation. Investigating the development of hearing in songbirds is therefore important, even though technically challenging. More broadly, there is accumulating evidence that some bird species use sounds beyond their known hearing range (especially towards high frequencies), which also calls for a reassessment of avian auditory perception.

Weaknesses

Rather than following validated protocols, the study presents many experimental flaws and two major methodological mistakes (see below), which invalidate all results on responses to frequency-specific tones in nestlings and those on vibration transmission to eggs, as well as largely underestimating hearing sensitivity. Accordingly, the study fails to detect a response in the majority of individuals tested with tones, including adults, and the results are overall inconsistent with previous studies in songbirds. The text throughout the preprint is also highly inaccurate, often presenting only part of the evidence or misrepresenting previous findings (both qualitatively and quantitatively; some examples are given below), which alters the conclusions.

Conclusion and impact

The conclusion from this study is not supported by the evidence. Even if the experiment had been performed correctly, there are well-recognised limitations and challenges of the method that likely explain the lack of response. The preprint fails to acknowledge that the method is well-known for largely underestimating hearing threshold (by 20-40dB in animals) and that it may not be suitable for a 1-gram hatchling. Unlike what is claimed throughout, including in the title, the failure to detect hearing sensitivity in this study does not invalidate all previous findings documenting the impacts of prenatal sound and noise on songbird development. The limitations of the approach and of this study are a much more parsimonious explanation. The incorrect results and interpretations, and the flawed representation of current knowledge, mean that this preprint regrettably creates more confusion than it advances the field.

Detailed assessment

For brevity, only some references are included below as examples, using, when possible, those cited in the preprint (DOI is provided otherwise). A full review of all the studies supporting the points below is beyond the scope of this assessment.

(A) Hearing experiment

The study uses the Auditory Brainstem Response (ABR), which measures minute electrical signals transmitted to the surface of the skull from the auditory nerve and nuclei in the brainstem. ABR is widely used, especially in humans, because it is non-invasive. However, ABR is also a lot less sensitive than other methods, and requires very specific experimental precautions to reliably detect a response, especially in extremely small animals and with high-frequency sounds, as here.

(1) Results on nestling frequency sensitivity are invalid, for failing to follow correct protocols:

The results on frequency testing in nestlings are invalid, since what might serve as a positive control did not work: in adults, no response was detected in a majority of individuals, at the core of their hearing range, with loud 95dB sounds (Figure S1), when testing frequency sensitivity with "tone burst".

This is mostly because the study used a stimulation duration 5 times larger than the norm. It used 25ms tone bursts, when all published avian studies (in altricial or precocial birds) used stimulation of 5ms or less (when using subdermal electrodes as here; e.g., cited: Brittan-Powell et al 2004; not cited: Brittan-Powell et al 2002 (doi: 10.1121/1.1494807), Henry & Lucas 2008 (doi: 10.1016/j.anbehav.2008.08.003)). Long stimulations do not make sense and are indeed known to interfere with the detection of an ABR response, especially at high frequencies, as, for example, explicitly tested and stated in Lauridsen et al 2021 (cited).

Adult response was then re-tested with a correct 5ms tone duration ("tone-pip"), which showed that, for the few individuals that responded to 25ms tones, thresholds were abnormally high (c.a. by 30dB; Figure 2C).<br /> Yet, no nestlings were retested with a correct protocol. There is therefore no valid data to support any conclusion on nestling frequency hearing. Under these circumstances, the fact that some nestlings showed a response to 25ms tones from day 8 would argue against them having very low sensitivity to sound.

(2) Responses to clicks underestimate hearing onset by several days:

Without any valid nestling responses to tones (see # 1), establishing the onset of hearing is not possible based on responses to clicks only, since responses to clicks occur at least 4 days after responses to tones during development (Saunders et al, 1973). Here, 60% of 4-day-old individuals responding to clicks means most would have responded to tones at and before 2 days post-hatch, had the experiment been done correctly.<br /> Responses to tones are indeed observed in other songbirds at 1day post-hatch (see #6).

In budgerigars, hearing onset occurs before 5 days post hatch, since responses to both clicks and tones were detectable at the first age tested at 5dph (Brittan-Powell et al, 2004).

(3) Experimental parameters chosen lower ABR detectability, specifically in younger birds:

Very fast stimulus repetition rate inhibits the ABR response, especially in young:

(a) The stimulus presentation rate (25 stim/ sec) is 6 times faster than zebra finch heat-calls, and 5 to 25 times faster than most previous studies in young birds (e.g., cited: Saunders et al 1973, 1974: 1 stim/sec or less; Katayama 1985: 3.3 clicks/sec; Brittan-Powell et al 2004: 4 stim/sec). Faster rates saturate the neurons and accordingly are known to decrease ABR amplitude and increase ABR latency, especially in younger animals with an immature nervous system. In birds, this occurs especially in the range from 5 to 30 stim/sec (e.g., cited: Saunder et al 1973, Brittan-Powell et al 2004). Values here with 25 rather than 1-4 stim/min are therefore underestimating true sensitivity.

(b) Averaging over only 400 measures is insufficient to reliably detect weak ABR signals:

The study uses 2 to 3 times fewer measures per stimulation type than the recommended value of 1,000 (e.g., Brittan-Powell et al 2002, 2024; Henry & Lucas 2008). This specifically affects the detection of weak signals, as in small hatchlings with tiny brains (adult zebra finches are 12-14g).

(c) Body temperature is not specified and strongly affects the ABR:

Controlling the body temperature of hatchlings of 1-4 grams (with a temperature probe under a 5mm-wide wing) would be very challenging. Low body temperature entirely eliminates the ABR, and even slight deviance from optimal temperature strongly increases wave latency and decreases wave amplitude (e.g., cited: Katayama 1985).

(d) Other essential information is missing on parameters known to affect the ABR:

This includes i) the weight of the animals, ii) whether and how the response signal was amplified and filtered, iii) how the automatised S/N>2 criteria compared to visual assessment for wave detection, and iv) what measures were taken to allow the correct placement of electrodes on hatchlings less than 5 grams.

(4) Results in adults largely underestimate sensitivity at high frequencies, and are not the correct reference point:

(a) Thresholds measured here at high frequencies for adults (using the correct stimulus duration, only done on adults) are 10-30dB higher than in all 3 other published ABR studies in adult zebra finches (cited: Zevin et al 2004; Amin et al 2007; not cited: Noirot et al 2011 (10.1121/1.3578452)), for both 4 and 6 kHz tone pips.

(b) The underlying assumption used throughout the preprint that hearing must be adult-like to be functional in nestlings does not make sense. Slower and smaller neural responses are characteristic of immature systems, but it does not mean signals are not being perceived.

(5) Failure to account for ABR underestimation leads to false conclusions:

(a) Whether the ABR method is suitable to assess hearing in very small hatchlings is unknown. No previous avian study has used ABR before 5 days post-hatch, and all have used larger bird species than the zebra finch.

(b) Even when performed correctly on large enough animals, the ABR systematically underestimates actual auditory sensitivity by 20-40 dB, especially at high frequencies, compared to behavioural responses (e.g., none cited: Brittan-Powell et al 2002, Henry & Lucas 2008, Noirot et al 2011). Against common practice, the preprint fails to account for this, leading to wrong interpretations. For example, in Figure 1G (comparing to heat call levels), actual hearing thresholds would be 30-40dB below those displayed. In addition, the "heat whistle" level displayed here (from the same authors) is 15dB lower than their second measure that they do not mention, and than measures obtained by others (unpublished data). When these two corrections are made - or even just the first one - the conclusion that heat-call sound levels are below the zebra finch hearing threshold does not hold.

(c) Rather than making appropriate corrections, the preprint uses a reference in humans (L180), where ABR is measured using a much more powerful method (multi-array EEG) than in animals, and from a larger brain. The shift of "10-20dB" obtained in humans is not applicable to animals.

(6) Results are inconsistent with previous findings in developing songbirds:

As expected from all of the above, results and conclusions in the preprint are inconsistent with findings in other songbirds, which, using other methods, show for example, auditory sensitivity in:

(a) zebra finch embryos, in response to song vs silence (not cited: Rivera et al 2018, doi: 10.1097/WNR.0000000000001187)

(b) flycatcher hatchlings at 2-3d post hatch (first age tested), across a wide range of frequencies (0.3 to 5kHz), at low to moderate sound levels (45-65dB) (cited: Aleksandrov and Dmitrieva 1992, not cited: Korneeva et al 2006 (10.1134/S0022093006060056)).

(c) songbird nestlings at 2-6d post hatch, which discriminate and behaviourally respond to relevant parental calls or even complex songs. This level of discrimination requires good hearing across frequencies (e.g., not cited: Korneeva et al 2006; Schroeder & Podos 2023 (doi: 10.1016/j.anbehav.2023.06.015)).

(d) zebra finch nestlings at 13d post-hatch, which show adult-like processing of songs in the auditory cortex (CNM) (Schroeder & Remage‐Healey 2021, doi: 10.1002/dneu.22802).

(e) zebra finch juveniles, which are able to perceive and learn song syllables at 5-7kHz (fundamental frequency) with very similar acoustic properties to heat calls, and also produced during inspiration (Goller & Daley 2001, doi: 10.1098/rspb.2001.1805).

NONE of these results - which contradict results and claims in the preprint - are mentioned. Instead, the preprint focuses on very slow-developing species (parrots and owls), which take 2-4 times longer than songbirds to fledge (cited: Brittan-Powell et al 2004; Köppl & Nickel 2007; Kraemer et al 2017).

(7) Results in figures are misreported in the text, and conclusions in the abstract and headers are not supported by the data:

For example:

(a) The data on Figure 1E shows that at 4 days old, 8 out of 13 nestlings (60%) responded to clicks, but the text says only 5/13 responded (L89). When 60% (4dph) and 90% (6dph) of individuals responded, the correct term would be that "most animals", rather than "some animals" responded (L89). Saying that ABR to loud sound appeared "in the majority only after one week" (L93) is also incorrect, given the data. It follows that the title of the paragraph is also erroneous.

(b) The hearing threshold is underestimated by 40dB at 6 and 8Kz on Fig 2C, not by "10-20dB" as reported in the text (L178).

(B) Egg vibration experiment

(8) Using airborne sound to vibrate eggs is biologically irrelevant:

The measurement of airborne sound levels to vibrate eggs misunderstands bone conduction hearing and is not biologically meaningful: zebra finch parents are in direct contact with the eggs when producing heat calls during incubation, not hovering in front of the nest. This misunderstanding affects all extrapolations from this study to findings in studies on prenatal communication.

(C) Misrepresentation of current knowledge

(9) Values from published papers are misreported, which reverses the conclusions:

Most critical examples:

(a) Preprint: "Zebra finch most sensitive hearing range of 1-to-4 kHz (Amin et al., 2007; Okanoya and Dooling, 1987; Yeh et al., 2023)" (L173).<br /> Actual values in the studies cited are:

1-to-7kHz, in Amin et al 2007 (threshold [=50dB with ABR] is the same at 7kHz and 1KHz).

1-to-6 kHz, in Okanoya and Dooling (the threshold [=30dB with behaviour] is actually lower at 6kHz than at 1KHz).

1-to-7kHz, in Yeh et al (threshold [=35-38dB with behaviour] is the same at 7kHz and 1KHz).

Note that zebra finch nestlings' begging calls peaking at 6kHz (Elie & Theunissen 2015, doi: 10.1007/s10071-015-0933-6), would fall 2kHz above the parents' best hearing range if it were only up to 4kHz.

(b) The preprint incorrectly states throughout (e.g., L139, L163, L248) that heat-calls are 7-10kHz, when the actual value is 6-10kHz in the paper cited (Katsis et al, 2018).

(c) Using the correct values from these studies, and heat-calls at 45 dB SLP (as measured by others (unpublished data), or as measured by the authors themselves, but which is not reported here (Anttonen et a,l 2025), the correct conclusion is that heat calls fall within the known zebra finch hearing range.

(10) Published evidence towards high-frequency hearing, including in early development, is systematically omitted:

(a) Other studies showing birds use high frequencies above the known avian hearing range are ignored. This includes oilbirds (7-23kHz; Brinklov et al 2017; by 1 of the preprint authors, doi: 10.1098/rsos.170255) and hummingbirds (10-20kHz; Duque et al 2020, doi: 10.1126/sciadv.abb9393), and in a lesser extreme, zebra finches' inspiratory song syllables at 5-7kHz (Goller & Dalley, 2001).

(b) The discussion of anatomical development (L228-241) completely omits the well-known fact that the avian basilar papilla develops from high to low frequencies (i.e., base to apex), which - as many have pointed out - is opposite to the low-to-high development of sensitivity (e.g., cited: Cohen & Fermin 1978; Caus Capdevila et al 2021).

(c) High frequency hearing in songbirds at hatching is several orders of magnitude better than in chickens and ducks at the same age, even though songbirds are altricial (e.g., at 4kHz, flycatcher: 47dB, chicken-duck: 90dB; at 5kHz, flycatcher: 65dB, chicken-duck: 115dB; Korneeva et al 2006, Saunders et al 1974). That is because Galliformes are low-frequency specialists, according to both anatomical and ecological evidence, with calls peaking at 0.8 to 1.2kHz rather than 2-6kHz in songbirds. It is incorrect to conclude that altricial embryos cannot perceive high frequencies because low-frequency specialist precocial birds do not (L250;261).

The references used to support the statement on a very high threshold for precocial birds above 6kHz are also wrong (L250). Katayama 1985 did not test embryos, nor frequency tones. Neither of these two references tested ducks.

(11) Incorrect statements do not reflect findings from the references cited

For example:

(a) "in altricial bird species hearing typically starts after hatching" (L12, in abstract), "with little to no functional hearing during embryonic stages (Woolley, 2017)." (L33).

There is no evidence, in any species, to support these statements. This is only a - commonly repeated - assumption, not actually based on any data. On the contrary, the extremely limited evidence to date shows the opposite, with zebra finch embryos showing ZENK activation in the auditory cortex in response to song playback (Rivera et al, 2018, not cited).

The book chapter cited (Woolley 2017) acknowledges this lack of evidence, and, in the context of song learning, provides as only references (prior to 2018), 2 studies showing that songbirds do not develop a normal song if the song tutor is removed before 10d post-hatch. That nestlings cannot memorise (to later reproduce) complex signals heard before d10 does not mean that they are deaf to any sound before day 10.

Studies showing hearing in young songbird nestlings (see point 6 above) also contradict these statements.

(b) "Zebra finch embryos supposedly are epigenetically guided to adapt to high temperatures by their parents high-frequency "heat calls" " (L36 and L135).

This is an extremely vague and meaningless description of these results, which cannot be assessed by readers, even though these results are presented as a major justification for the present study. Rather than giving an interpretation of what "supposedly" may occur, it would be appropriate to simply synthesize the empirical evidence provided in these papers. They showed that embryonic exposure to heat-calls, as opposed to control contact calls, alters a suite of physiological and behavioural traits in nestlings, including how growth and cellular physiology respond to high temperatures. This also leads to carry-over effects on song learning and reproductive fitness in adulthood.

(c) "The acoustic communication in precocial mallard ducks depends specifically on the low-frequency auditory sensitivity of the embryo (Gottlieb, 1975)" (L253)

The study cited (Gottlieb, 1975) demonstrates exactly the opposite of this statement: it shows that duckling embryos, not only perceive high frequency sounds (relative to the species frequency range), but also NEED this exposure to display normal audition and behaviour post-hatch. Specifically, it shows that duckling embryos deprived of exposure to their own high-frequency calls (at 2 kHz), failed to identify maternal calls post-hatch because of their abnormal insensitivity to higher frequencies, which was later confirmed by directly testing their auditory perception of tones (Dimitrieva & Gottlieb, 1994).

(12) Considering all of the mistakes and distortions highlighted above, it would be very premature to conclude, based on these results and statements, that altricial avian embryos are not sensitive to sound. This study provides no actual scientific ground to support this conclusion.

Author Response:

We thank all reviewers for their time and effort to carefully review our paper and for the constructive comments on our manuscript. Below we outline our planned revisions to the public reviews of the three reviewers.

In our revision, we will include more details regarding our ABR measurements (including temperature, animal metadata), analysis (including filter settings) and lay out a much more detailed motivation for our ABR signal design. Furthermore, we will provide a more detailed discussion on the caveats of the technique and the interpretation of ABR data in general and our data specifically. Furthermore, we will add more discussion on differences between ABR based audiograms and behavioural data. The authors have extensive experience with the ABR technique and are well aware of its limitations, but also its strengths for use in animals that cannot be trained on behavioural tasks such as the very young zebra finches in this study. These additions will strengthen our paper. We think our conclusions remain justified by our data.

Reviewer #1 and #2:

We thank both reviewers for their positive words and suggested improvements. The planned general improvements listed above will take care of all suggestions and comments in the public review.

Reviewer #3:

We thank the reviewer for the detailed critique of our manuscript and many suggestions for improvement. The planned general improvements listed above will take care of many of the suggestions and comments listed in the public review. Here we will highlight a few first responses that we will address in detail in our resubmission.

The reviewer’s major critiques can be condensed to the following four points.

(1) ABR cannot be done in such small animals.

This critique is unfounded. ABR measures the summed activity in the auditory pathway, and with smaller distance from brainstem to electrodes in small animals, the ABR signals are expected to have higher amplitude and consequently better SNR.  Thus, smaller animals should lead to higher amplitude ABR signals. We have successfully recorded ABR in animals smaller than 2 DPH zebra finches to support this claim (zebrafish (Jørgensen et al., 2012), 10 mm froglets (Goutte et al., 2017) and 5 mm salamanders (Capshaw et al., 2020). It is more surprising the technique still provides robust signals even in very large animals such as Minke whales (Houser et al., 2024).

(2) The ABR methods used does not follow protocol for other published work in birds. Particularly the 25 ms long duration tone bursts may have underestimated high frequency hearing.

There is no fixed protocol for ABR measurements, and several studies of bird ABR have used as long or even longer durations. Longer-duration signals were chosen deliberately and are necessary to have a sufficient number of cycles and avoid frequency splatter at our lowest frequencies used (see Lauridsen et al., 2021).

(3) Sensitivity data should be corrected from ABR to behavioural data.

We present the results of our measurements on hearing sensitivity using ABR, and ABR based thresholds are generally less sensitive than thresholds based on behavioural studies (presented in Fig 2c). Correcting for these measurements to behavioural thresholds is of course possible, but presenting only the corrected thresholds would be a misrepresentation of our sensitivity data. Even so it should be done only within species and age group and such data is currently not available. In our revision, we will include elaborate discussion on this topic.

(4) Results are inconsistent with papers in developing songbirds.

We agree that our results do not support and even question the claims in earlier work. These papers however do either 1) not measure hearing physiology or 2) do so in different species. To our best knowledge there is presently no data published on the auditory physiology development in songbird embryos. Our data are consistent with what is known about the physiology of auditory development in all birds studied so far. We will provide a detailed discussion on this topic in our revision.

References

Capshaw et al. (2020) J Exp Biol 223: jeb236489

Goutte et al. (2017) Sci Rep 7: 12121, doi 10.1038/s41598-017-12145-5

Houser et al. (2024) Science 386, 902-906. DOI:10.1126/science.ado7580).

Jørgensen et al. (2012) Adv Exp Med Biol 730: 117-119

Lauridsen et al (2021) J Exp Biol 224: jeb237313. https://doi.org/10.1242/jeb.237313

eLife Assessment

This study provides evidence for distinct neurotransmitter release modalities between two subclasses of dopaminergic neurons in the olfactory bulb. Specifically, it demonstrates dendritic neurotransmitter release in anaxonic neurons and axonal release in axon-bearing neurons. The presence of GABAergic self-inhibition in anaxonic neurons further underscores the functional divergence between these subtypes. Overall, the manuscript presents solid evidence and offers biologically important insights into the organization and function of dopaminergic circuits within the olfactory bulb.

Reviewer #1 (Public review):

Summary:

Dorrego-Rivas et al. investigated two different DA neurons and their neurotransmitter release properties in the main olfactory bulb. They found that the two different DA neurons in mostly glomerular layers have different morphologies as well as electrophysiological properties. The anaxonic DA neurons are able to self-inhibit but the axon-bearing ones are not. The findings are interesting and important to increase the understanding both of the synaptic transmissions in the main olfactory bulb and the DA neuron diversity. However, there are some major questions that the authors need to address to support their conclusions.

(1) It is known that there are two types of DA neurons in the glomerular layer with different diameters and capacitances (Kosaka and Kosaka, 2008; Pignatelli et al., 2005; Angela Pignatelli and Ottorino Belluzzi, 2017). In this manuscript, the authors need to articulate better which layer the imaging and ephys recordings took place, all glomerular layers or with an exception. Meanwhile, they have to report the electrophysiological properties of their recordings, including capacitances, input resistance, etc.

(2) It is understandable that recording the DA neurons in the glomerular layer is not easy. However, the authors still need to increase their n's and repeat the experiments at least three times to make their conclusion more solid. For example (but not limited to), Fig 3B, n=2 cells from 1 mouse. Fig.4G, the recording only has 3 cells.

(3) The statistics also use pseudoreplicates. It might be better to present the biology replicates, too.

(4) In Figure 4D, the authors report the values in the manuscript. It is recommended to make a bar graph to be more intuitive.

(5) In Figure 4F and G, although the data with three cells suggest no phenotype, the kinetics looked different. So, the authors might need to explore that aside from increasing the n.

(6) Similarly, for Figure 4I and J, L and M, it is better to present and analyze it like F and G, instead of showing only the after-antagonist effect.

Comments on revisions:

In the rebuttal, the authors argued that it had been extremely hard to obtain recordings stable enough for before-and-after effects on the same cell. Alternatively, they could perform the before-and-after comparison on different cells.

Reviewer #2 (Public review):

Summary:

This study provides novel insights into the neurotransmitter release mechanisms employed by two distinct subclasses of dopaminergic neurons in the olfactory bulb (OB). The findings suggest that anaxonic neurons primarily release neurotransmitters through their dendrites, whereas axon-bearing neurons predominantly release neurotransmitters via their axons. Furthermore, the study reveals that anaxonic neurons exhibit self-inhibitory behavior, indicating that closely related neuronal subclasses may possess specialized roles in sensory processing.

Strengths:

This study introduces a novel and significant concept, demonstrating that two closely related neuron subclasses can exhibit distinct patterns of neurotransmitter release. Therefore, this finding establishes a valuable framework for future investigations into the functional diversity of neuronal subclasses and their contributions to sensory processing. Furthermore, these findings offer fundamental insights into the neural circuitry of the olfactory bulb, enhancing our understanding of sensory information processing within this critical brain region.

Weaknesses:

The reliance on synaptophysin-based presynaptic structures raises minor concerns about whether these structures represent functional synapses.

Comments on revisions:

Most of the concerns have been addressed by the authors, and there are no further comments about this manuscript.

Author response:

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

Reviewer #1 (Public review):

This Reviewer was positive about the study, stating ‘The findings are interesting and important to increase the understanding both of the synaptic transmissions in the main olfactory bulb and the DA neuron diversity.’ They provided a number of helpful suggestions for improving the paper, which we have incorporated as follows:

(1) It is known that there are two types of DA neurons in the glomerular layer with different diameters and capacitances (Kosaka and Kosaka, 2008; Pignatelli et al., 2005; Angela Pignatelli and Ottorino Belluzzi, 2017). In this manuscript, the authors need to articulate better which layer the imaging and ephys recordings took place, all glomerular layers or with an exception. Meanwhile, they have to report the electrophysiological properties of their recordings, including capacitances, input resistance, etc.

We thank the Reviewer for this clarification. Indeed, the two dopaminergic cell types we study here correspond directly to the subtypes previously identified based on cell size. Our previous work showed that axon-bearing OB DA neurons have significantly larger somas than their anaxonic neighbours (Galliano et al. 2018), and we replicate this important result in the present study (Figure 3D). In terms of electrophysiological correlates of cell size, we now provide full details of passive membrane properties in the new Supplementary Figure 4, as requested. Axon-bearing DA neurons have significantly lower input resistance and show a non-significant trend towards higher cell capacitance. Both features are entirely consistent with the larger soma size in this subtype. We apologise for the oversight in not fully describing previous categorisations of OB DA neurons, and have now added this information and the appropriate citations to the Introduction (lines 56 to 59 of the revised manuscript). 

In terms of cell location, all cells in this study were located in the OB glomerular layer. We sampled the entire glomerular layer in all experiments, including the glomerular/EPL border where the majority of axon-bearing neurons are located (Galliano et al. 2018). This is now clarified in the Materials and Methods section (lines 535 to 537 and 614 to 616 of the revised manuscript).

(2) It is understandable that recording the DA neurons in the glomerular layer is not easy. However, the authors still need to increase their n's and repeat the experiments at least three times to make their conclusion more solid. For example (but not limited to), Fig 3B, n=2 cells from 1 mouse. Fig.4G, the recording only has 3 cells.

Despite the acknowledged difficulty of these experiments, we have now added substantial extra data to the study as requested. We have increased the number of cells and animals to further support the following findings:

Fig 3B: we now have n=5 cells from N=3 mice. We have created a new Supplementary Figure 1 to show all the examples.

Figure 4G: we now have n=6 cells from N=4 mice.

Figure 5G: we now have n=3 cells from N=3 mice.

The new data now provide stronger support for our original conclusions. In the case of auto-evoked inhibition after the application of D1 and D2 receptor antagonists, a nonsignificant trend in the data suggests that, while dopamine is clearly not necessary for the response, it may play a small part in its strength. We have now included this consideration in the Results section (lines 256 to 264 of the revised manuscript).

(3) The statistics also use pseudoreplicates. It might be better to present the biology replicates, too.

Indeed, in a study focused on the structural and functional properties of individual neurons, we performed all comparisons with cell as the unit of analysis. This did often (though not always) involve obtaining multiple data points from individual mice, but in these low-throughput experiments n was never hugely bigger than N. The potential impact of pseudoreplicates and their associated within-animal correlations was therefore low. We checked this in response to the Reviewer’s comment by running parallel nested analyses for all comparisons that returned significant differences in the original submission. These are the cases in which we would be most concerned about potential false positive results arising from intra-animal correlations, which nested tests specifically take into account (Aarts et al., 2013). In every instance we found that the nested tests also reported significant differences between anaxonic and axonbearing cell types, thus fully validating our original statistical approach. We now report this in the relevant section of the Materials and Methods (lines 686 to 691 of the revised manuscript).

(4) In Figure 4D, the authors report the values in the manuscript. It is recommended to make a bar graph to be more intuitive.

This plot does already exist in the original manuscript. We originally describe these data to support the observation that an auto-evoked inhibition effect exists in anaxonic neurons (corresponding to now lines 240 to 245 of the revised manuscript). We then show them visually in their entirety when we compare them to the lack of response in axon-bearing neurons, depicted in Figure 5C. We still believe that this order of presentation is most appropriate for the flow of information in the paper, so have maintained it in our revised submission.

(5) In Figure 4F and G, although the data with three cells suggest no phenotype, the kinetics looked different. So, the authors might need to explore that aside from increasing the n.

We thank the Reviewer for this suggestion. To quantify potential changes in the autoevoked inhibition response kinetics, we fitted single exponential functions and compared changes in the rate constant (k; Methods, lines 650 to 652 of the revised manuscript). Overall, we observed no consistent or significant change in rate constant values after adding DA receptor antagonists. This finding is now reported in the Results section (lines 260 to 263 of the revised manuscript) and shown in a new Supplementary Figure 3.

(6) Similarly, for Figure 4I and J, L and M, it is better to present and analyze it like F and G, instead of showing only the after-antagonist effect.

We agree that the ideal scenario would have been to perform the experiments in Figure 4J and 4M the same way as those in Figure 4G, with a before vs after comparison. Unfortunately, however, this was not practically possible. 

When attempting to apply carbenoxelone to already-patched cells, we found that this drug highly disrupted the overall health and stability of our recordings immediately after its application. This is consistent with previous reports of similar issues with this compound (e.g. Connors 2012, Epilepsy Currents; Tovar et al., 2009, Journal of Neurophysiology). After many such attempts, the total yield of this experiment was one single cell from one animal. Even so, as shown in the traces below, we were able to show that the auto-evoked inhibition response was not eliminated in this specific case:

Author response image 1.

Traces of an AEI response recorded before (magenta) and after (green) the application of carbenoxolone (n=1 cell from N=1 mouse).

In light of these issues, we instead followed published protocols in applying the carbenoxolone directly in the bath without prior recording for 20 minutes (following Samailova et al., 2003, Journal of Neurochemistry) and ran the protocol after that time. Given that our main question was to ask whether gap junctions were strictly necessary for the presence of any auto-evoked inhibition response, our positive findings in these experiments still allowed us to draw clear conclusions.

In contrast, the issue with the NKCC1 antagonist bumetanide was time. As acknowledged by this Reviewer, obtaining and maintaining high-quality patch recordings from OB DA neurons is technically challenging. Bumetanide is a slow-acting drug when used to modify neuronal chloride concentrations, because in addition to the time it takes to reach the neurons and effectively block NKCC1, the intracellular levels of chloride subsequently change slowly. Studies using this drug in slice physiology experiments typically use an incubation time of at least 20 minutes (e.g. Huberfeld et al., 2007, Journal of Neuroscience), which was incompatible with productive data collection in OB DA neurons. Again, after many unsuccessful efforts, we were forced instead to include bumetanide in the bath without prior recording for 20-30 minutes. As with the carbenoxolone experiment, our goal here was to establish whether autoevoked inhibition was in any way retained in the presence of this drug, so our positive result again allowed us to draw clear conclusions.

Reviewer #1 (Recommendations for the authors):

(1) I suggest the authors reconsider the terminology. For example, they use "strikingly" in their title. The manuscript reported two different transmitter release strategies but not the mechanisms, and the word "strikingly" is not professional, either.

We appreciate the Reviewer’s attention to clarity and tone in the manuscript title, and have nevertheless decided to retain the original wording. The almost all-or-nothing differences between closely related cell types shown in structural and functional properties here (Figures 3F & 5C) are pronounced, extremely clear and easily spotted – all properties appropriate for the word ‘striking.’ In addition, we note that the use of this term is not at all unprofessional, with a PubMed search for ‘strikingly’ in the title of publications returning over 200 hits.

(2) Similarly, almost all confocal scopes are 3D because images can be taken at stacks. So "3D confocal" is misleading.

We understand that this is misleading. We have now replaced the sentence ‘Example snapshot of a 3D confocal stack of…’ by ‘Example confocal images of…’ in all the figure legends that apply.

(3) It is recommended to present the data in bar graphs with data dots instead of showing the numbers in the manuscript directly.

We agree entirely, and now present data plots for all comparisons reported in the study (Supplementary Figures 2, 4 and 5).

Reviewer #2 (Recommendations for the authors):

(1) Several experiments report notably small sample sizes, such as in Figures 3B and 5G, where data from only 2 cells derived from 1-2 mice are presented. Figures 4E-G also report the experimental result only from 3 cells derived from 3 mice. To enhance the statistical robustness and reliability of the findings, these experiments should be replicated with larger sample sizes.

As per our response to Reviewer 1’s comment #2 above, and to directly address the concern that some evidence was ‘incomplete’, we have now added significant extra data and analysis to this revised submission (Figures 4 and 5; and Supplementary Figure 1). We believe that this has further enhanced the robustness and reliability of our findings, as requested.

(2) The authors utilize vGAT-Cre for Figures 1-3 and DAT-tdTomato for Figures 4-5, raising concerns about consistency in targeting the same population of dopaminergic neurons. It remains unclear whether all OB DA neurons express vGAT and release GABA. Clarification and additional evidence are needed to confirm whether the same neuronal population was studied across these experiments.

Although we indeed used different mouse lines to investigate structural and functional aspects of transmitter release, we can be very confident that both approaches allowed us to study the same two distinct DA cell types being compared in this paper. Existing data to support this position are already clear and strong, so in this revision we have focused on the Reviewer’s suggestion to clarify the approaches we chose.

First, it is well characterised that in mouse and many other species all OB DA neurons are also GABAergic. This has been demonstrated comprehensively at the level of neurochemical identity and in terms of dopamine/GABA co-release, and is true across both small-soma/anaxonic and large-soma/axon-bearing subclasses (Kosaka & Kosaka 2008; 2016; Maher & Westbrook 2008; Borisovska et al., 2013; Vaaga et al., 2016; Liu et al. 2013). To specifically confirm vGAT expression, we have also now provided additional single-cell RNAseq data and immunohistochemical label in a revised Figure 1 (see also Panzanelli et al., 2007, now referenced in the paper, who confirmed endogenous vGAT colocalisation in TH-positive OB neurons). Most importantly, by using vGAT-cre mice here we were able to obtain sufficient numbers of both anaxonic and axon-bearing DA neurons among the vGAT-cre-expressing OB population. We could unambiguously identify these cells as dopaminergic because of their expression of TH protein which, due to the absence of noradrenergic neurons in the OB, is a specific and comprehensive marker for dopaminergic cells in this brain region (Hokfelt et al., 1975; Rosser et al., 1986; Kosaka & Kosaka 2016). Crucially, both axon-bearing and anaxonic OB DA subtypes strongly express TH (Galliano et al., 2018, 2021). We have now added additional text to the relevant Results section (lines 99 to 108 of the revised manuscript) to clarify these reasons for studying vGAT-cre mice here.

We were also able to clearly identify and sample both subtypes of OB DA neuron using DAT-tdT mice. Our previous published work has thoroughly characterised this exact mouse line at the exact ages studied in the present paper (Galliano et al., 2018; Byrne et al., 2022). We know that DAT-tdT mice provide rather specific label for TH-expressing OB DA neurons (75% co-localisation; Byrne et al., 2022), but most importantly we know which non-DA neurons are labelled in this mouse line and how to avoid them. All nonTH-expressing but tdT-positive cells in juvenile DAT-tdT mice are small, dimly fluorescent and weakly spiking neurons of the calretinin-expressing glomerular subtype (Byrne et al., 2022). These cells are easily detected during physiological recordings, and were excluded from our study here. This information is now provided in the relevant Methods section (lines 616 to 619 of the revised manuscript, also referenced in lines 236 to 240 of the results section), and we apologise for its previous omission. Finally, we have shown both structurally and functionally that both axon-bearing and anaxonic OB DA subtypes are labelled in DAT-tdT mice (Galliano et al., 2018, Tufo et al., 2025; present study). Overall, these additional clarifications firmly establish that the same neuronal populations were indeed studied across our experiments.

(3) The low TH+ signal in Figure 1D raises questions regarding the successful targeting of OB DA neurons. Further validation, such as additional staining, is required to ensure that the targeted neurons are accurately identified.

As noted in our response to the previous comment, TH is a specific marker for dopaminergic neurons in the mouse OB, and is widely used for this purpose. Labelling for TH in our tissue is extremely reliable, and in fact gives such strong signal that we were forced to reduce the primary antibody concentration to 1:50,000 to prevent bleedthrough into other acquisition channels. Even at this concentration it was extremely straightforward to unambiguously identify TH-positive cells based on somatic immunofluorescence. We recognise, however, that the original example image in Figure 1D was not sufficiently clear, and have now provided a new example which illustrates the TH-based identification of these cells much more effectively. 

(4) Estimating the total number of dopaminergic neurons in the olfactory bulb, along with the relative proportions of anaxonic and axon-bearing neuron subtypes, would provide valuable context for the study. Presenting such data is crucial to underscore the biological significance of the findings.

This information has already been well characterised in previous studies. Total dopaminergic cell number in the OB is ~90,000 (Maclean & Shipley, 1988; Panzanelli et al., 2007; Parrish-Aungst et al., 2007). In terms of proportions, anaxonic neurons make up the vast majority of these cells, with axon-bearing neurons representing only ~2.5% of all OB dopaminergic neurons at P28 (Galliano et al., 2018). Of course, the relatively low number of the axon-bearing subtype does not preclude its having a potentially large influence on glomerular networks and sensory processing, as demonstrated by multiple studies showing the functional effects of inter-glomerular inhibition (Kosaka & Kosaka, 2008; Liu et al., 2013; Whitesell et al., 2013; Banerjee et al., 2015). This information has now been added to the Introduction (line 47 and lines 59 to 62 of the revised manuscript).

(5) The authors report that in-utero injection was performed based on the premise that the two subclasses of dopaminergic neurons in the olfactory bulb are generated during embryonic development. However, it remains unclear whether in-utero injection is essential for distinguishing between these two subclasses. While the manuscript references a relevant study, the explanation provided is insufficient. A more detailed justification for employing in-utero injection would enhance the manuscript's clarity and methodological rigor.

We apologise for the lack of clarity in explaining the approach. In utero injection is not absolutely essential for distinguishing between the two subclasses, but it does have two major advantages. 1) Because infection happens before cells migrate to their final positions, it produces sparse labelling which permits later unambiguous identification of individual cells’ processes; and 2) Because both subclasses are generated embryonically (compared to the postnatal production of only anaxonic DA neurons), it allows effective targeting of both cell types. We have now expanded the relevant section of the Results to explain the rationale for our approach in more detail (lines 109 to 116 of the revised manuscript).

(6) In Figures 1A and 4A, it appears that data from previously published studies were utilized to illustrate the differential mRNA expression in dopaminergic neurons of the olfactory bulb. However, the Methods section and the manuscript lack a detailed description of how these dopaminergic neurons were classified or analyzed. Given that these figures contribute to the primary dataset, providing additional explanation and context is essential to ensure clarity of the findings.

We apologise for the lack of clarity. We have now extended the part of the methods referring to the RNAseq data analysis (lines 666 to 678 of the revised manuscript). 

(7) In Figure 2C, anaxonic dopamine neurons display considerable variability in the number of neurotransmitter release sites, with some neurons exhibiting sparse sites while others exhibit numerous sites. The authors should address the potential biological or methodological reasons for this variability and discuss its significance.

We thank the Reviewer for highlighting this feature of our data. We have now outlined potential methodological reasons for the variability, whilst also acknowledging that it is consistent with previous reports of presynaptic site distributions in these cells (Kiyokage et al., 2017; Results, lines 169 to 172 of the revised manuscript). We have also added a brief discussion of the potential biological significance (Discussion, lines 446 to 450).

(8) In the images used to differentiate anaxonic and axon-bearing neurons, the soma, axons, and dendrites are intermixed, making it difficult to distinguish structures specific to each subclass. Employing subclass-specific labeling or sparse labeling techniques could enhance clarity and accuracy in identifying these structures.

Distinguishing these structures is indeed difficult, and was the main reason we used viral label to produce sparse labelling (see response to comment #5 above). In all cases we were extremely careful, including cells only when we could be absolutely certain of their anaxonic or axon-bearing identity, and could also be certain of the continuity of all processes. Crucially, while the 2D representations we show in our figures may suggest a degree of intermixing, we performed all analyses on 3D image stacks, significantly improving our ability to accurately assign structures to individual cells. We have now added extra descriptions of this approach in the relevant Methods section (lines 546 to 548 of the revised manuscript).

(9) In Figure 3, the soma area and synaptophysin puncta density are compared between axon-bearing and anaxonic neurons. However, the figure only presents representative images of axon-bearing neurons. To ensure a fair and accurate comparison, representative images of both neuron subtypes should be included.

The original figures did include example images of puncta density (or lack of puncta) in both cell types (Figure 2B and Figure 3E). For soma area, we have now included representative images of axon-bearing and anaxonic neurons with an indication of soma area measurement in a new Supplementary Figure 2A.

(10) In Figure 4B, the authors state that gephyrin and synaptophysin puncta are in 'very close proximity.' However, it is unclear whether this proximity is sufficient to suggest the possibility of self-inhibition. Quantifying the distance between gephyrin and synaptophysin puncta would provide critical evidence to support this claim. Additionally, analyzing the distribution and proportion of gephyrinsynaptophysin pairs in close proximity would offer further clarity and strengthen the interpretation of these findings.

We thank the Reviewer for raising this issue. We entirely agree that the example image previously shown did not constitute sufficient evidence to claim either close proximity of gephyrin and synaptophysin puncta, nor the possibility of self-inhibition. We are not in a position to perform a full quantitative analysis of these spatial distributions, nor do we think this is necessary given previous direct evidence for auto-evoked inhibition in OB dopaminergic cells (Smith and Jahr, 2002; Murphy et al., 2005; Maher and Westbrook, 2008; Borisovska et al., 2013) and our own demonstration of this phenomenon in anaxonic neurons (Figure 4). We have therefore removed the image and the reference to it in the text. 

(11) In Figures 4J and 4M, the effects of the drugs are presented without a direct comparison to the control group (baseline control?). Including these baseline control data is essential to provide a clear context for interpreting the drug effects and to validate the conclusions drawn from these experiments.

We appreciate the Reviewer’s attention to this important point. As this concern was also raised by Reviewer 1 (their point #6), we have provided a detailed response fully addressing it in our replies to Reviewer 1 above. 

(12) In Lines 342-344, the authors claim that VMAT2 staining is notoriously difficult. However, several studies (e.g., Weihe et al., 2006; Cliburn et al., 2017) have successfully utilized VMAT2 staining. Moreover, Zhang et al., 2015 - a reference cited by the authors - demonstrates that a specific VMAT2 antibody effectively detects VMAT2. Providing evidence of VMAT2 expression in OB DA neurons would substantiate the claim that these neurons are GABA-co-releasing DA neurons and strengthen the study's conclusions.

As noted in response to this Reviewer’s comment #2 above, there is clear published evidence that OB DA neurons are GABA- and dopamine-releasing cells. These cells are also known to express VMAT2 (Cave et al., 2010; Borisovska et al., 2013; Vergaña-Vera et al., 2015). We do not therefore believe that additional evidence of VMAT2 expression is necessary to strengthen our study’s conclusions. We did make every effort to label VMAT2-positive release sites in our neurons, but unfortunately all commercially available antibodies were ineffective. The successful staining highlighted by the Reviewer was either performed in the context of virally driven overexpression (Zhang et al., 2015) or was obtained using custom-produced antibodies (Weihe et al., 2006; Cliburn et al., 2017). We have now modified the Discussion text to provide more clarification of these points (lines 393 to 395 of the revised manuscript).

eLife Assessment

This important theoretical study shows that active hexatic topological defects in epithelia enable collective cell flows. Within the general limitations of coarse-grained hydrodynamic models in fully capturing cell-scale behavior, the study provides compelling evidence supporting its conclusions. These findings will be of interest to both biophysicists studying collective cell behaviors and biologists investigating epithelial flows during development.

Reviewer #1 (Public review):

Summary:

This paper investigates the physical mechanisms underlying cell intercalation, which then enables collective cell flows in confluent epithelia. The authors show that T1 transitions (the topological transitions responsible for cell intercalation) correspond to the unbinding of groups of hexatic topological defects. Defect unbinding, and hence cell intercalation and collective cell flows, are possible when active stresses in the tissue are extensile. This result helps to rationalize the observation that many epithelial cell layers have been found to exhibit extensile active nematic behavior.

Strengths:

The authors obtain their results based on a combination of active hexanematic hydrodynamics and a multiphase field (MPF) model for epithelial layers, whose connection is a strength of the paper. With the hydrodynamic approach, the authors find the active flow fields produced around hexatic topological defects, which can drive defect unbinding. Using the MPF simulations, the authors show that T1 transitions tend to localize close to hexatic topological defects.

Reviewer #2 (Public review):

Summary:

This paper studies the role of hexatic defects in the collective migration of epithelia. The authors emphasize that epithelial migration is driven by cell intercalation events and not just isolated T1 events, and analyze this through the lens of hexatic topological defects. Finally, the authors study the effect of active and passive forces on the dynamics of hexatic defects using analytical results, and numerical results in both continuum and phase-field models. The results are very interesting, and highlight new ways of studying epithelial cell migration through the analysis of the binding and unbinding of hexatic defects.

Strengths:

(1) The authors convincingly argue that intercalation events are responsible for collective cell migration, and that these events are accompanied by the formation and unbinding of hexatic topological defects. (2) The authors clearly explain the dynamics of hexatic defects during T1 transitions, and demonstrate the importance of active and passive forces during cell migration. (3) The paper thorougly studies the T1 transition throught the viewpoint of hexatic defects. A continuum model approach to study T1 transitions in cell layers is novel and can lead to valuable new insights.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

This paper investigates the physical mechanisms underlying cell intercalation, which then enables collective cell flows in confluent epithelia. The authors show that T1 transitions (the topological transitions responsible for cell intercalation) correspond to the unbinding of groups of hexatic topological defects. Defect unbinding, and hence cell intercalation and collective cell flows, are possible when active stresses in the tissue are extensile. This result helps to rationalize the observation that many epithelial cell layers have been found to exhibit extensile active nematic behavior.

Strengths

The authors obtain their results based on a combination of active hexanematic hydrodynamics and a multiphase field (MPF) model for epithelial layers, whose connection is a strength of the paper. With the hydrodynamic approach, the authors find the active flow fields produced around hexatic topological defects, which can drive defect unbinding. Using the MPF simulations, the authors show that T1 transitions tend to localize close to hexatic topological defects.

We are grateful to Reviewer #1, for appreciating and highlighting the strengths of work.

Weaknesses

Citations are sometimes not comprehensive. Cases of contractile behavior found in collective cell flows, which would seemingly contradict some of the authors’ conclusions, are not discussed.

I encourage the authors to address the comments and questions below.

We are thankful to Reviewer #1, for their questions and comments. We have addressed them point by point below, and have amended the manuscript accordingly.

(1) In Equation 1, what do the authors mean by the cluster’s size ℓ? How is this quantity defined? The calculations in the Methods suggest that ℓ indicates the distance between the p-atic defects and the center of the T1 cell cluster, but this is not clearly defined.

We are thank Reviewer #1 for their question. We define the cluster size as the initial distance between the center of the quadrupole and any defect (see Methods). In a primary cell cluster, where cells themselves are the defects, the cluster’s size is the distance between the center of the central junction and the center of any cell in the cluster. Hence, this is half the diameter of an cell which, for example in a typical, confluent MDCK epithelial monolayer, would be about 10µm. We have added this clarification in the definition of the cluster size, above Eq. (1).

(2) The multiphase field model was developed and reviewed already, before the Loewe et al. 2020 paper that the authors cite. Earlier papers include Camley et al. PNAS 2014, Palmieri et al. Sci. Rep. 2015, Mueller et al. PRL 2019, and Peyret et al. Biophys. J. 2019, as reviewed in Alert and Trepat. Annu. Rev. Condens. Matter Phys. 2020.

We thank the referee for their suggestion to incorporate further MPF literature. We have done so in the amended manuscript.

(3) At what time lag is the mean-squared displacement in Figure 3f calculated? How does the choice of a lag time affect these data and the resulting conclusions?

The scatter plot in Fig. 3f was constructed by dividing the system into square subregions of size ∆ℓ = 35 l.u., each containing approximately 4 cells. For each subregion, we analyzed a time window of ∆t = 25 × 10³ iterations, measuring both the normalized mean square displacement of cells (relative to the subregion area ∆ℓ²) and the average defect density. The normalized displacement is calculated as m.s.d. , where t∗ denotes the start time of the observation window. We chose the time window ∆t used to compute the mean square displacement to match the characteristic duration of T1 events and defect lifetimes in our simulations. Observation times much longer (∆t > 35 × 10³) than the typical T1 event duration would cause the two sets of data points to merge into a single group, suggesting no correlation between cell motility and defect density beyond defect life-time.

(4) The authors argue that their results provide an explanation for the extensile behavior of cell layers. However, there are also examples of contractile behavior, such as in Duclos et al., Nat. Phys., 2017 and in P´erez-Gonz´alez et al., Nat. Phys., 2019. In both cases, collective cell flows were observed, which in principle require cell intercalations. How would these observations be rationalized with the theory proposed in this paper? Can these experiments and the theory be reconciled?

The contractile or extensile nature of stress in epithelia depends crucially on the specific tissue type and its biological context. Different cell populations, depending on their position along the epithelial/mesenchymal spectrum, can exhibit either contractile or extensile behaviors. Our theory applies to tissues where hexatic order dominates at the cellular scale, particularly in confluent systems where neighbor exchanges occur primarily through T1 transitions. In contrast, the systems studied by Duclos et al., Nat. Phys. (2018) and Perez-Gonzalez et al. (Nat. Phys., 2019) exhibit nematic order at the cellular level, meaning their dynamics are governed by fundamentally different mechanisms. Since our framework is derived for hexatic-dominated tissues, it does not directly apply to those cases, though a hybrid hexanematic descriptions previously developed by some of the authors in Armengol-Collado et al. eLife 13:e86400 (2024) could help reconcile these observations. In general, a key distinction must be made between the contractility of individual cells and the extensile/contractile nature of the collective force network. To illustrate this, consider a cell exerting a 6- fold symmetric force distribution: each vertex force arises from an imbalance in junctional tensions with neighboring cells, which are themselves contractile due to actomyosin activity. However, the resulting vertex forces can be either contractile or extensile depending on network geometry and tension distribution. This is captured in our coarse-grained description [see Armengol-Collado et al. eLife 13:e86400 (2024)], where the active stress emerges from higher-order moments of cellular forces. Specifically, the deviatoric part of the hexatic active stress tensor , where is the cell radius, the number cell density and the intensity of cellular tension. The negative sign of the coefficient of the active stress shows that the active stress is extensile—consistently with observations in various epithelial systems (e.g., Saw et al., Nature 2017; Blanch-Mercader et al., Phys. Rev. Lett. 2018). Finally, we note that the connection between cellular-scale forces and large-scale extensility has been rationalized in other contexts, such as active nematics (Balasubramaniam et al., Nat. Mater. 2021).

Reviewer #2 (Public Review):

This paper studies the role of hexatic defects in the collective migration of epithelia. The authors emphasize that epithelial migration is driven by cell intercalation events and not just isolated T1 events, and analyze this through the lens of hexatic topological defects. Finally, the authors study the effect of active and passive forces on the dynamics of hexatic defects using analytical results, and numerical results in both continuum and phase-field models.

The results are very interesting and highlight new ways of studying epithelial cell migration through the analysis of the binding and unbinding of hexatic defects.

We are grateful to Reviewer #2, for their interest and for emphasizing the novelty of our work.

Strengths

(1) The authors convincingly argue that intercalation events are responsible for collective cell migration, and that these events are accompanied by the formation and unbinding of hexatic topological defects.

(2) The authors clearly explain the dynamics of hexatic defects during T1 transitions, and demonstrate the importance of active and passive forces during cell migration.

(3) The paper thoroughly studies the T1 transition through the viewpoint of hexatic defects. A continuum model approach to study T1 transitions in cell layers is novel and can lead to valuable new insights.

We thank the Reviewer for their kind and supporting words, and for highlighting the clarity, persuasiveness, and thoroughness.

Weaknesses

(1) The authors could expand on the dynamics of existing hexatic defects during epithelial cell migration, in addition to how they are created during T1 transitions.

We thank the referee for their comment. The detailed analysis of dislocation-pair unbinding modes and their statistical impact on the transition to collective migration is comprehensively addressed in our subsequent work Puggioni et al., arXiv:2502.09554. In the present study, we focus specifically on the fundamental mechanism enabling dislocation unbinding: active extensile stresses generate flows that drive dislocation pairs apart, while passive elastic stresses tend to pull them together (Krommydas et al., Phys. Rev. Lett. 2023; Armengol- Collado et al., arXiv:2502.13104). When active forces dominate over passive restoring forces, the dislocations unbind. This represents a crucial distinction from classical Berezinskii–Kosterlitz–Thouless or Kosterlitz–Thouless–Halperin–Nelson–Youn transitions, where thermal fluctuations drive defect unbinding. In our system, the process is fundamentally activity-driven. Nevertheless, the resulting state - characterized by unbound defects and collective migration - bears strong analogy to the melting transition in equilibrium systems. We emphasize that the dynamics of passive defects has been previously examined in Krommydas et al., Phys. Rev. Lett. 2023. A discussion of these aspects can be found in the Appendix “Numerical simulations of defect annihilation and unbinding”.

(2) The different terms in the MPF model used to study cell layer dynamics are not fully justified. In particular, it is not clear why the model includes self-propulsion and rotational diffusion in addition to nematic and hexatic stresses, and how these quantities are related to each other.

We thank the referee for their comment. The MPF model’s terms (e.g., self-propulsion, rotational diffusion), reflect the stochastic, deformable nature of cells as active droplets migrating with near-constant speed. We emphasize that self-propulsion is the only non-equilibrium mechanism in our model — no additional active stresses (nematic or hexatic) are imposed. We have clarified this point in the revised manuscript and expanded our discussion of the MPF model.

(3) The authors could provide some physical intuition on what an active extensile or contractile term in the hexatic order parameter means, and how this is related to extensility and contractility in active nematics and/or for cell layers.

We thank the referee for their comment. As we explain in the reply to comment [4] of Reviewer #1, the contractile or extensile nature of stress in epithelia depends crucially on the specific tissue type and its biological context. Different cell populations, depending on their position along the epithelial/mesenchymal spectrum, can exhibit either contractile or extensile behaviors. Our theory applies to tissues where hexatic order dominates at the cellular scale, particularly in confluent systems where neighbor exchanges occur primarily through T1 transitions. In contrast, the systems studied by Duclos et al., Nat. Phys. (2018) and Perez-Gonzalez et al. (Nat. Phys., 2019) exhibit nematic order at the cellular level, meaning their dynamics are governed by fundamentally different mechanisms. Since our framework is derived for hexatic-dominated tissues, it does not directly apply to those cases, though a hybrid hexanematic descriptions previously developed by some of the authors in Armengol-Collado et al. eLife 13:e86400 (2024) could help reconcile these observations. In general, a key distinction must be made between the contractility of individual cells and the extensile/contractile nature of the collective force network. To illustrate this, consider a cell exerting a 6-fold symmetric force distribution: each vertex force arises from an imbalance in junctional tensions with neighboring cells, which are themselves contractile due to actomyosin activity. However, the resulting vertex forces can be either contractile or extensile depending on network geometry and tension distribution. This is captured in our coarse-grained description [see Armengol-Collado et al. eLife 13:e86400 (2024)], where the active stress emerges from higher-order moments of cellular forces. Specifically, the deviatoric part of the hexatic active stress tensor , where is the cell radius, the number cell density and the intensity of cellular tension. The negative sign of the coefficient of the active stress shows that the active stress is extensile—consistently with observations in various epithelial systems (e.g., Saw et al., Nature 2017; Blanch-Mercader et al., Phys. Rev. Lett. 2018). Finally, we note that the connection between cellular-scale forces and large-scale extensility has been rationalized in other contexts, such as active nematics (Balasubramaniam et al., Nat. Mater. 2021).

Recommendations for the Authors: Reviewer #2 (Recommendations for the Authors):

(1) The authors point out that hexatic topological defects are produced in quadrupoles (L109). Does this also mean that these defects can be annihilated only in quadrupoles as well? In the same vein, are hexatic defects always bound in pairs, as suggested by the schematics, or is it possible to observe an isolated hexatic defect?

We thank the referee for their question. Hexatic disclinations (the defect monopoles discussed in this work), much like electrons and positrons, can annihilate in any number of neutral charge configuration (dipole, quadrupole, octupole, etc.). Unbinding a pair of hexatic disinclination, however, costs much more energy than unbinding a quadrupole to dipoles. Hence isolated defects appear in abundance only in late, fully disordered phase, where the system has completely “melted”. For more details on how defect unbinding modes affect tissue dynamics, please see our subsequent work Puggioni et al., arXiv:2502.09554.

(2) Could you clarify if the flows described in Figures 2(a)-(b), panel (i) are driven by a passive backflow term without activity? Could you compare the magnitudes of these flows compared to the typical active terms?

We thank the referee for their question. In panel 2(b) there is only passive backflow. In 2(a) instead, both terms are included, and are in a regime of parameters where the active flow overcomes the active flow (and hence the active force overcomes the passive force as delineated in the discussions section). In turn, the magnitude of the passive flows, is studied in detail in our previous work Krommydas et al., (Phys. Rev. Lett. 2023).

(3) Could you clarify how the continuum hexatic model and MPF model are related to each other? What are the similarities and differences in the dynamics of these models?

We thank the referee for this insightful question. A key point of our work is precisely that the continuum hexatic model and the MPF (Multi-Phase Field) model are distinct in nature.

The MPF model is an established agent-based framework used to simulate tissue dynamics at the cellular level. It captures individual cell behaviors and interactions through phase-field variables. In our work, we use the MPF model as a benchmark to extract statistical features of tissue dynamics, such as defect motion and orientational correlations. In contrast, our continuum hexatic model is a coarse-grained hydrodynamic theory that describes the dynamics of orientational order in active tissues. It is built on symmetry principles and conservation laws, and it does not rely on microscopic cell-level details. Instead, it captures the collective behavior of the system through a hexatic order parameter and its coupling to flow and activity.

Despite their conceptual differences, the MPF model and our hydrodynamic theory exhibit similar statistical features. This agreement—also observed in the independent study by Jain et al. (Phys. Rev. Res. 2024)—provides strong support for the validity and generality of our continuum description.

(4) When multiple references by the same author and year are cited using alphabets, the second alphabet is not in bold e.g. Giomi et al., 2022b, a in Line 75, and others.

We are grateful to the referee carefully going through the manuscript and pointing out these typos. We have corrected them in the amended manuscript.

Reviewer #3 (Public Review):

In this manuscript, the authors discuss epithelial tissue fluidity from a theoretical perspective. They focus on the description of topological transitions whereby cells change neighbors (T1 transitions). They explain how such transitions can be described by following the fate of hexatic defects. They first focus on a single T1 transition and the surrounding cells using a hydrodynamic model of active hexatics. They show that successful T1 intercalations, which promote tissue fluidity, require a sufficiently large extensile hexatic activity in the neighborhood of the cells attempting a T1 transition. If such activity is contractile or not sufficiently extensile, the T1 is reversed, hexatic defects annihilate, and the epithelial network configuration is unchanged. They then describe a large epithelium, using a phase field model to describe cells. They show a correlation between T1 events and hexatic defects unbinding, and identify two populations of T1 cells: one performing T1 cycles (failed T1), and not contributing to tissue migration, and one performing T1 intercalation (successful T1) and leading to the collective cell migration.

Strengths

The manuscript is scientifically sound, and the variety of numerical and analytical tools they use is impressive. The approach and results are very interesting and highlight the relevance of hexatic order parameters and their defects in describing tissue dynamics.

We thank the Reviewer for recognizing the scientific soundness of the manuscript, the breadth of numerical and analytical tools employed, as well as their interest in our work.

Weaknesses

(1) Goal and message of the paper. (a) In my opinion, the article is mainly theoretical and should be presented as such. For instance, their conclusions and the consequences of their analysis in terms of biology are not extremely convincing, although they would be sufficient for a theory paper oriented to physicists or biophysicists. The choice of journal and potential readership should be considered, and I am wondering whether the paper structure should be re-organized, in order to have side-by-side the methods and the results, for instance (see also below).

We thank the referee for their criticism. In response, we have made an effort to reword certain parts of the manuscript. As with any theoretical study, the biological implications of our work can only be fully assessed through experimental validation — a prospect we look forward to. Nevertheless, we have submitted our work to the subsection of Physics of Life, which we believe is perfectly suited to our content.

(b) Currently, the two main results sections are somewhat disconnected, because they use different numerical models, and because the second section only marginally uses the results from the first section to identify/distinguish T1.

We thank the referee, for their comment. In the second section we are using statistics from the MPF model, to support the analytical and numerical findings of our hydrodynamic theory of cell intercalation. In the time between our submission, further qualitative evidence have been brought to light in the work of Jain et al. (Phys. Rev. Res. 2024).

(2) Quite surprisingly, the authors use a cell-based model to describe the macroscopic tissuescale behavior, and a hydrodynamic model to describe the cell-based events. In particular, their hydrodynamic description (the active hexatic model) is supposed to be a coarse-grained description, valid to capture the mesoscopic physics, and yet, they use it to describe cellscale events (T1 transitions). For instance, what is the meaning of the velocity field they are discussing in Figure 2? This makes me question the validity of the results of their first part.

We thank the referee for their comment. There are many excellent discrete models of epithelial tissues in the literature (e.g., Bi et al., Phys. Rev. X 2016; Pasupalak et al., Soft Matter 2020; Graner et al., Phys. Rev. Lett. 1992), each capturing essential biological features such as cell division, apoptosis and sorting. While these models have provided invaluable insights, our work takes a different approach by developing a continuum theory aimed at describing epithelial dynamics at two levels: (1) mesoscopic intercalation events and (2) macroscopic collective migration. Crucially, our goal is not to replicate a specific discrete model — which would risk constructing a “model of a model” — but rather to derive a hydrodynamic description of tissue dynamics grounded in symmetry principles and conservation laws. Along this logic, the velocity field in our theory should be interpreted as an Eulerian (continuum) velocity, representing the coarse-grained flow of the tissue rather than the Lagrangian motion of individual cells. This distinction is central to our framework, which operates at scales where cellular details are averaged out, yet retains the essential physics of hexatic order and active stresses. We validate our predictions against the Multiphase Field (MPF) model. [We thank Reviewer 1 for their suggestion to incorporate further MPF literature.] Furthermore, Jain et al. (Phys. Rev. Res. 2024) have used the MPF to predict flow patterns around T1 transitions and obtained results compatible with those of our hydrodynamic theory. From this comparison we can conclude that both the MPF and our theory are able to capture the same aspect of cell intercalation in epithelial layer. This, however, does not imply that other discrete models of epithelia can reproduce this aspect too, nor that our theory is specifically tailored to the MPF model. We have clarified these points in the revised manuscript and expanded our discussion of the MPF model.

(3) The quality of the numerical results presented in the second part (phase field model) could be improved. (a) In terms of analysis of the defects. It seems that they have all the tools to compare their cell-resolved simulations and their predictions about how a T1 event translates into defects unbinding. However, their analysis in Figure 3e is relatively minimal: it shows a correlation between T1 cells and defects. But it says nothing about the structure and evolution of the defects, which, according to their first section, should be quite precise.

We thank the referee for their comment. Further qualitative evidence have been brought to light in the work of Jain et al. (Phys. Rev. Res. 2024), were the exact flow pattern predicted by our hydrodynamic theory is obtained, in the MPF, around cells undergoing T1 rearrangements.

(b) In terms of clarity of the presentation. For instance, in Figure 3f, they plot the mean-square displacement as a function of a defect density. I thought that MSD was a time-dependent quantity: they must therefore consider MSD at a given time, or averaged over time. They should be explicit about what their definition of this quantity is.

We thank the referee for raising this point. As clarified in our response to Reviewer 1, point 3, the mean square displacement (MSD) plotted in Fig. 3f is computed over a fixed time window of ∆t = 25×103 iterations, chosen to match the typical duration of T1 events and defect lifetimes. [See also reply to Reviewer #1, point (3).] The MSD is normalized by the subregion area and averaged over time within each window. We have now made this explicit in the amended version of the manuscript.

(c) In terms of statistics. For instance, Figure 3g is used to study the role of rotational diffusion on the average time between T1s. The error bars in this figure are huge and make their claims hardly supported. Their claim of a ”monotonic decay” of the average time between intercalations is also not fully supported given their statistics.

We appreciate the Reviewer’s comment regarding the statistical robustness of Fig. 3g. While we acknowledge that the error bars are substantial – reflecting the inherent variability in cell intercalation dynamics – the yellow curve does exhibit a consistent downward trend in the average time between T1 transitions as rotational diffusion increases. This monotonic decrease is visible across the entire range of variation of the rotational diffusion Dr, and is statistically supported when considering the trend over independent simulations. To address this concern, we have revised the main text to adjusted the wording: instead of stating that “the former is a monotonically decreasing function of Dr,” we now write that “the former displays a decreasing trend with Dr,” which better reflects the statistical variability while preserving the observed behavior.

Reviewer #3 (Recommendations for the Authors):

(1) Section 1 is difficult to follow due to multiple reasons: early but delayed definitions, unclear use of T1 intercalation vs. T1 cycles, disconnected figures and unclear simulation descriptions. We recommend including simulation setup details earlier and restructuring the flow of arguments.

We thank the referee for their comment. We have made an effort in rewording and clarifying things in our amended manuscript. We are slightly confused by what they mean by “early but delayed definitions”, if they could clarify, we would be happy to amend the position and phrasing of these definitions accordingly.

(2) It could be useful to have an additional figure early on defining schematically hexatic defects and an illustration showing an epithelium (or a simulation), similar to what the authors have produced in some of their other publications on this topic.

We thank the referee for their comment. Figures 3c and 3d show what a hexatic defect looks like in a simulation of the epithelium. Following the referee’s recommendation, we have added a note in the caption of figure 3, citing our work were we show the same defects in MDCK epithelial monolayers (Armengol et al., Nat. Phys. 2023).

(3) Minor points and typos:

Line 88: the bond between vertices shrinks, not the vertices.

Figure 1: the 1/6 is displayed as 1 6 (fraction bar missing).

Line 232: “and order” → “one/an order”.

Line 237: Fig. 3g) → Fig. 3g

Line 298: ”nu” and ”v” hard to distinguish in eLife font.

Methods: define all notation clearly (e.g., tensor product exponent, D/Dt in Eq. 3c).

Methods: ”cell orientation, coarse-graining and topological defects” section is difficult to follow, schematic would help.

Line 457 onward: unclear how panels (ii-iv) of Fig. 2ab are obtained.

Line 480 onward: not referenced in main text.

Figure 2: “avalancHe” typo.

Figure 2 caption: “cell intercalaTION” typo.

Movies are neither referenced nor explained.

Figure 5 and 6 are not referenced in the main text.

We thank the referee for their detailed read of the paper. We have corrected all typos.

eLife Assessment

This important work attempts to understand observed variability in oral shedding of SARS-CoV-2 and suggests that routine clinical factors are not determinative. The evidence supporting the conclusion is solid though the limited clinical heterogeneity of the included cohorts, the lack of COVID vaccination, and the absence of comprehensive viral load data for model training, makes the results difficult to generalize to contemporaneous COVID-19 conditions. This study may be of interest to virologists, public health officials and clinicians.

Reviewer #1 (Public Review):

Summary:

This study by Park and colleagues uses longitudinal saliva viral load data from two cohorts (one in the US and one in Japan from a clinical trial) in the pre-vaccine era to subset viral shedding kinetics and then use machine learning to attempt to identify clinical correlates of different shedding patterns. The stratification method identifies three separate shedding patterns discriminated by peak viral load, shedding duration, and clearance slope. The authors also assess micro-RNAs as potential biomarkers of severity but do not identify any clear relationships with viral kinetics.

Strengths:

The cohorts are well developed, the mathematical model appears to capture shedding kinetics fairly well, the clustering seems generally appropriate, and the machine learning analysis is a sensible, albeit exploratory approach. The micro-RNA analysis is interesting and novel.

Reviewer #2 (Public Review):

Summary:

This study argues it has found that it has stratified viral kinetics for saliva specimens into three groups by the duration of "viral shedding"; the authors could not identify clinical data or microRNAs that correlate with these three groups.

Strengths:

The question of whether there is a stratification of viral kinetics is interesting.

Reviewer #3 (Public Review):

The article presents a comprehensive study on the stratification of viral shedding patterns in saliva among COVID-19 patients. The authors analyze longitudinal viral load data from 144 mildly symptomatic patients using a mathematical model, identifying three distinct groups based on the duration of viral shedding. Despite analyzing a wide range of clinical data and micro-RNA expression levels, the study could not find significant predictors for the stratified shedding patterns, highlighting the complexity of SARS-CoV-2 dynamics in saliva. The research underscores the need for identifying biomarkers to improve public health interventions and acknowledges several limitations, including the lack of consideration of recent variants, the sparsity of information before symptom onset, and the focus on symptomatic infections.

The manuscript is well-written, with the potential for enhanced clarity in explaining statistical methodologies. This work could inform public health strategies and diagnostic testing approaches.

Comments on the revised version from the editor:

The authors comprehensively addressed the concerns of all 3 reviewers. We are thankful for their considerable efforts to do so. Certain limitations remain unavoidable such as the lack of immunologic diversity among included study participants and lack of contemporaneous variants of concern.

One remaining issue is the continued use of the target cell limited model which is sufficient in most cases, but misses key datapoints in certain participants. In particular, viral rebound is poorly described by this model. Even if viral rebound does not place these cases in a unique cluster, it is well understood that viral rebound is of clinical significance.

In addition, the use of microRNAs as a potential biomarker is still not fully justified. In other words, are there specific microRNAs that have a pre-existing mechanistic basis for relating to higher or lower viral loads? As written it still feels like microRNA was included in the analysis simply because the data existed.

Author response:

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

Reviewer #1 (Public review)

Summary:

This study by Park and colleagues uses longitudinal saliva viral load data from two cohorts (one in the US and one in Japan from a clinical trial) in the pre-vaccine era to subset viral shedding kinetics and then use machine learning to attempt to identify clinical correlates of different shedding patterns. The stratification method identifies three separate shedding patterns discriminated by peak viral load, shedding duration, and clearance slope. The authors also assess micro-RNAs as potential biomarkers of severity but do not identify any clear relationships with viral kinetics.

Strengths:

The cohorts are well developed, the mathematical model appears to capture shedding kinetics fairly well, the clustering seems generally appropriate, and the machine learning analysis is a sensible, albeit exploratory approach. The micro-RNA analysis is interesting and novel.

Weaknesses:

The conclusions of the paper are somewhat supported by the data but there are certain limitations that are notable and make the study's findings of only limited relevance to current COVID-19 epidemiology and clinical conditions.

We sincerely appreciate the reviewer’s thoughtful and constructive comments, which have been invaluable in improving the quality of our study. We have carefully revised the manuscript to address all points raised.

(1) The study only included previously uninfected, unvaccinated individuals without the omicron variant. It has been well documented that vaccination and prior infection both predict shorter duration shedding. Therefore, the study results are no longer relevant to current COVID-19 conditions. This is not at all the authors' fault but rather a difficult reality of much retrospective COVID research.

Thank you for your comment. We agree with the review’s comment that some of our results could not provide insight into the current COVID-19 conditions since most people have either already been infected with COVID-19 or have been vaccinated. We revised our manuscript to discuss this (page 22, lines 364-368). Nevertheless, we believe it is novel that we have extensively investigated the relationship between viral shedding patterns in saliva and a wide range of clinical and microRNA data, and that developing a method to do so remains important. This is important for providing insight into early responses to novel emerging viral diseases in the future. Therefore, we still believe that our findings are valuable.

(2) The target cell model, which appears to fit the data fairly well, has clear mechanistic limitations. Specifically, if such a high proportion of cells were to get infected, then the disease would be extremely severe in all cases. The authors could specify that this model was selected for ease of use and to allow clustering, rather than to provide mechanistic insight. It would be useful to list the AIC scores of this model when compared to the model by Ke.

Thank you for your feedback and suggestion regarding our mathematical model. As the reviewer pointed out, in this study, we adopted a simple model (target cell-limited model) to focus on reconstruction of viral dynamics and stratification of shedding patterns rather than exploring the mechanism of viral infection in detail. Nevertheless, we believe that the target cell-limited model provides reasonable reconstructed viral dynamics as it has been used in many previous studies. We revised manuscript to clarify this point (page 10, lines 139-144). Also, we revised our manuscript to provide more detailed description of the model comparison along with information about AIC (page 10, lines 130-135).

(3) Line 104: I don't follow why including both datasets would allow one model to work better than the other. This requires more explanation. I am also not convinced that non-linear mixed effects approaches can really be used to infer early model kinetics in individuals from one cohort by using late viral load kinetics in another (and vice versa). The approach seems better for making populationlevel estimates when there is such a high amount of missing data.

Thank you for your feedback. We recognized that our explanation was insufficient by your comment. We intended to describe that, rather than comparing performance of the two models, data fitting can be performed with same level for both models by including both datasets. We revised the manuscript to clarify this point (page 10, lines 135-139).

Additionally, we agree that nonlinear mixed effects models are a useful approach for performing population-level estimates of missing data. On the other hand, in addition, the nonlinear mixed effects model has the advantage of making the reasonable parameter estimation for each individual with not enough data points by considering the distribution of parameters of other individuals. Paying attention to these advantages, we adopted a nonlinear mixed effects model in our study. We also revised the manuscript to clarify this (page 27, lines 472-483).

(4) Along these lines, the three clusters appear to show uniform expansion slopes whereas the NBA cohort, a much larger cohort that captured early and late viral loads in most individuals, shows substantial variability in viral expansion slopes. In Figure 2D: the upslope seems extraordinarily rapid relative to other cohorts. I calculate a viral doubling time of roughly 1.5 hours. It would be helpful to understand how reliable of an estimate this is and also how much variability was observed among individuals.

We appreciate your detailed feedback on the estimated up-slope of viral dynamics. As the reviewer noted, the pattern differs from that observed in the NBA cohort, which may be due to their measurement of viral load from upper respiratory tract swabs. In our estimation, the mean and standard deviation of the doubling time (defined as ln2/(𝛽𝑇₀𝑝𝑐⁻¹ − 𝛿)) were 1.44 hours and 0.49 hours, respectively. Although direct validation of these values is challenging, several previous studies, including our own, have reported that viral loads in saliva increase more rapidly than in the upper respiratory tract swabs, reaching their peak sooner. Thus, we believe that our findings are consistent with those of previous studies. We revised our manuscript to discuss this point with additional references (page 20, lines 303-311).

(5) A key issue is that a lack of heterogeneity in the cohort may be driving a lack of differences between the groups. Table 1 shows that Sp02 values and lab values that all look normal. All infections were mild. This may make identifying biomarkers quite challenging.

Thank you for your comment regarding heterogeneity in the cohort. Although the NFV cohort was designed for COVID-19 patients who were either mild or asymptomatic, we have addressed this point and revised the manuscript to discuss it (page 21, lines 334-337).

(6) Figure 3A: many of the clinical variables such as basophil count, Cl, and protein have very low pre-test probability of correlating with virologic outcome.

Thank you for your comment regarding some clinical information we used in our study. We revised our manuscript to discuss this point (page 21, lines 337-338).

(7) A key omission appears to be micoRNA from pre and early-infection time points. It would be helpful to understand whether microRNA levels at least differed between the two collection timepoints and whether certain microRNAs are dynamic during infection.

Thank you for your comment regarding the collection of micro-RNA data. As suggested by the reviewer, we compared micro-RNA levels between two time points using pairwise t-tests and Mann-Whitney U tests with FDR correction. As a result, no micro-RNA showed a statistically significant difference. This suggests that micro-RNA levels remain relatively stable during the course of infection, at least for mild or asymptomatic infection, and may therefore serve as a biomarker independent of sampling time. We have revised the manuscript to include this information (page 17, lines 259-262).

(8) The discussion could use a more thorough description of how viral kinetics differ in saliva versus nasal swabs and how this work complements other modeling studies in the field.

We appreciate the reviewer’s thoughtful feedback. As suggested, we have added a discussion comparing our findings with studies that analyzed viral dynamics using nasal swabs, thereby highlighting the differences between viral dynamics in saliva and in the upper respiratory tract. To ensure a fair and rigorous comparison, we referred to studies that employed the same mathematical model (i.e., Eqs.(1-2)). Accordingly, we revised the manuscript and included additional references (page 20, lines 303-311).

Furthermore, we clarified the significance of our study in two key aspects. First, it provides a detailed analysis of viral dynamics in saliva, reinforcing our previous findings from a single cohort by extending them across multiple cohorts. Second, this study uniquely examines whether viral dynamics in saliva can be directly predicted by exploring diverse clinical data and micro-RNAs. Notably, cohorts that have simultaneously collected and reported both viral load and a broad spectrum of clinical data from the same individuals, as in our study, are exceedingly rare. We revised the manuscript to clarify this point (page 20, lines 302-311).

(9) The most predictive potential variables of shedding heterogeneity which pertain to the innate and adaptive immune responses (virus-specific antibody and T cell levels) are not measured or modeled.

Thank you for your comment. We agree that antibody and T cell related markers may serve as the most powerful predictors, as supported by our own study [S. Miyamoto et al., PNAS (2023), ref. 24] as well as previous reports. While this point was already discussed in the manuscript, we have revised the text to make it more explicit (page 21, lines 327-328).

(10) I am curious whether the models infer different peak viral loads, duration, expansion, and clearance slopes between the 2 cohorts based on fitting to different infection stage data.

Thank you for your comment. We compared features between 2 cohorts as reviewer suggested. As a result, a statistically significant difference between the two cohorts (i.e., p-value ≤ 0.05 from the t-test) was observed only at the peak viral load, with overall trends being largely similar. At the peak, the mean value was 7.5 log₁₀ (copies/mL) in the Japan cohort and 8.1 log₁₀ (copies/mL) in the Illinois cohort, with variances of 0.88 and 0.87, respectively, indicating comparable variability.

Reviewer #2 (Public review)

Summary:

This study argues it has found that it has stratified viral kinetics for saliva specimens into three groups by the duration of "viral shedding"; the authors could not identify clinical data or microRNAs that correlate with these three groups.

Strengths:

The question of whether there is a stratification of viral kinetics is interesting.

Weaknesses:

The data underlying this work are not treated rigorously. The work in this manuscript is based on PCR data from two studies, with most of the data coming from a trial of nelfinavir (NFV) that showed no effect on the duration of SARS-CoV-2 PCR positivity. This study had no PCR data before symptom onset, and thus exclusively evaluated viral kinetics at or after peak viral loads. The second study is from the University of Illinois; this data set had sampling prior to infection, so has some ability to report the rate of "upswing." Problems in the analysis here include:

We are grateful to the reviewer for the constructive feedback, which has greatly enhanced the quality of our study. In response, we have carefully revised the manuscript to address all comments.

The PCR Ct data from each study is treated as equivalent and referred to as viral load, without any reports of calibration of platforms or across platforms. Can the authors provide calibration data and justify the direct comparison as well as the use of "viral load" rather than "Ct value"? Can the authors also explain on what basis they treat Ct values in the two studies as identical?

Thank you for your comment regarding description of viral load data. We recognized the lack of explanation for the integration of viral load data by reviewer's comment. We calculated viral load from Ct value using linear regression equations between Ct and viral load for each study's measurement method, respectively. We revised the manuscript to clarify this point in the section of Saliva viral load data in Methods.

The limit of detection for the NFV PCR data was unclear, so the authors assumed it was the same as the University of Illinois study. This seems a big assumption, as PCR platforms can differ substantially. Could the authors do sensitivity analyses around this assumption?

Thank you for your comment regarding the detection limit for viral load data. As reviewer suggested, we conducted sensitivity analysis for assumption of detection limit for the NFV dataset. Specifically, we performed data fitting in the same manner for two scenarios: when the detection limit of NFV PCR was lower (0 log₁₀ copies/mL) or higher (2 log₁₀ copies/mL) than that of the Illinois data (1.08 log₁₀ copies/mL), and compared the results.

As a result, we obtained largely comparable viral dynamics in most cases (Supplementary Fig 6). When comparing the AIC values, we observed that the AIC for the same censoring threshold was 6836, whereas it increased to 7403 under the low censoring threshold and decreased to 6353 under the higher censoring threshold. However, this difference may be attributable to the varying number of data points treated as below the detection limit. Specifically, when the threshold is set higher, more data are treated as below the detection limit, which may result in a more favorable error calculation. To discuss this point, we have added a new figure (Supplementary Fig 6) and revised the manuscript accordingly (page 25, lines 415-418).

The authors refer to PCR positivity as viral shedding, but it is viral RNA detection (very different from shedding live/culturable virus, as shown in the Ke et al. paper). I suggest updating the language throughout the manuscript to be precise on this point.

We appreciate the reviewer’s feedback regarding the terminology used for viral shedding. In response, we have revised all instances of “viral shedding” to “viral RNA detection” throughout the manuscript as suggested.

Eyeballing extended data in Figure 1, a number of the putative long-duration infections appear to be likely cases of viral RNA rebound (for examples, see S01-16 and S01-27). What happens if all the samples that look like rebound are reanalyzed to exclude the late PCR detectable time points that appear after negative PCRs?

We sincerely thank the reviewer for the valuable suggestion. In response, we established a criterion to remove data that appeared to exhibit rebound and subsequently performed data fitting

(see Author response image 1 below). The criterion was defined as: “any data that increase again after reaching the detection limit in two measurements are considered rebound and removed.” As a result, 15 out of 144 cases were excluded due to insufficient usable data, leaving 129 cases for analysis. Using a single detection limit as the criterion would have excluded too many data points, while defining the criterion solely based on the magnitude of increase made it difficult to establish an appropriate “threshold for increase.”

The fitting result indicates that the removal of rebound data may influence the fitting results; however, direct comparison of subsequent analyses, such as clustering, is challenging due to the reduced sample size. Moreover, the results can vary substantially depending on the criterion used to define rebound, and establishing a consistent standard remains difficult. Accordingly, we retained the current analysis and have added a discussion of rebound phenomena in the Discussion section as a limitation (page 22, lines 355-359). We once again sincerely appreciate the reviewer’s insightful and constructive suggestion.

Author response image 1.

Comparison of model fits before and after removing data suspected of rebound. Black dots represent observed measurements, and the black and yellow curves show the fitted viral dynamics for the full dataset and the dataset with rebound data removed, respectively.

There's no report of uncertainty in the model fits. Given the paucity of data for the upslope, there must be large uncertainty in the up-slope and likely in the peak, too, for the NFV data. This uncertainty is ignored in the subsequent analyses. This calls into question the efforts to stratify by the components of the viral kinetics. Could the authors please include analyses of uncertainty in their model fits and propagate this uncertainty through their analyses?

We sincerely appreciate the reviewer’s detailed feedback on model uncertainty. To address this point, we revised Extended Fig 1 (now renumbered as Supplementary Fig 1) to include 95% credible intervals computed using a bootstrap approach. In addition, to examine the potential impact of model uncertainty on stratified analyses, we reconstructed the distance matrix underlying stratification by incorporating feature uncertainty. Specifically, for each individual, we sampled viral dynamics within the credible interval and averaged the resulting feature, and build the distance matrix using it. We then compared this uncertainty-adjusted matrix with the original one using the Mantel test, which showed a strong correlation (r = 0.72, p < 0.001). Given this result, we did not replace the current stratification but revised the manuscript to provide this information through Result and Methods sections (page 11, lines 159-162 and page 28, lines 512-519). Once again, we are deeply grateful for this insightful comment.

The clinical data are reported as a mean across the course of an infection; presumably vital signs and blood test results vary substantially, too, over this duration, so taking a mean without considering the timing of the tests or the dynamics of their results is perplexing. I'm not sure what to recommend here, as the timing and variation in the acquisition of these clinical data are not clear, and I do not have a strong understanding of the basis for the hypothesis the authors are testing.

We appreciate the reviewers' feedback on the clinical data. We recognized that the manuscript lacked description of the handling of clinical data by your comment. In this research, we focused on finding “early predictors” which could provide insight into viral shedding patterns. Thus, we used clinical data measured in the earliest time (date of admission) for each patient. Another reason is that the date of admission is the almost only time point at which complete clinical data without any missing values are available for all participants. We revised our manuscript to clarify this point (page 5, lines 90-95).

It's unclear why microRNAs matter. It would be helpful if the authors could provide more support for their claims that (1) microRNAs play such a substantial role in determining the kinetics of other viruses and (2) they play such an important role in modulating COVID-19 that it's worth exploring the impact of microRNAs on SARS-CoV-2 kinetics. A link to a single review paper seems insufficient justification. What strong experimental evidence is there to support this line of research?

We appreciate the reviewer’s comments regarding microRNA. Based on this feedback, we recognized the need to clarify our rationale for selecting microRNAs as the analyte. The primary reason was that our available specimens were saliva, and microRNAs are among the biomarkers that can be reliably measured in saliva. At the same time, previous studies have reported associations between microRNAs and various diseases, which led us to consider the potential relevance of microRNAs to viral dynamics, beyond their role as general health indicators. To better reflect this context, we have added supporting references (page 17, lines 240-243).

Reviewer #3 (Public review)

The article presents a comprehensive study on the stratification of viral shedding patterns in saliva among COVID-19 patients. The authors analyze longitudinal viral load data from 144 mildly symptomatic patients using a mathematical model, identifying three distinct groups based on the duration of viral shedding. Despite analyzing a wide range of clinical data and micro-RNA expression levels, the study could not find significant predictors for the stratified shedding patterns, highlighting the complexity of SARS-CoV-2 dynamics in saliva. The research underscores the need for identifying biomarkers to improve public health interventions and acknowledges several limitations, including the lack of consideration of recent variants, the sparsity of information before symptom onset, and the focus on symptomatic infections. 

The manuscript is well-written, with the potential for enhanced clarity in explaining statistical methodologies. This work could inform public health strategies and diagnostic testing approaches. However, there is a thorough development of new statistical analysis needed, with major revisions to address the following points:

We sincerely appreciate the thoughtful feedback provided by Reviewer #3, particularly regarding our methodology. In response, we conducted additional analyses and revised the manuscript accordingly. Below, we address the reviewer’s comments point by point.

(1) Patient characterization & selection: Patient immunological status at inclusion (and if it was accessible at the time of infection) may be the strongest predictor for viral shedding in saliva. The authors state that the patients were not previously infected by SARS-COV-2. Was Anti-N antibody testing performed? Were other humoral measurements performed or did everything rely on declaration? From Figure 1A, I do not understand the rationale for excluding asymptomatic patients. Moreover, the mechanistic model can handle patients with only three observations, why are they not included? Finally, the 54 patients without clinical data can be used for the viral dynamics fitting and then discarded for the descriptive analysis. Excluding them can create a bias. All the discarded patients can help the virus dynamics analysis as it is a population approach. Please clarify. In Table 1 the absence of sex covariate is surprising.

We appreciate the detailed feedback from the reviewer regarding patient selection. We relied on the patient's self-declaration to determine the patient's history of COVID-19 infection and revised the manuscript to specify this (page 6, lines 83-84).

In parameter estimation, we used the date of symptom onset for each patient so that we establish a baseline of the time axis as clearly as possible, as we did in our previous works. Accordingly, asymptomatic patients who do not have information on the date of symptom onset were excluded from the analysis. Additionally, in the cohort we analyzed, for patients excluded due to limited number of observations (i.e., less than 3 points), most patients already had a viral load close to the detection limit at the time of the first measurement. This is due to the design of clinical trial, as if a negative result was obtained twice in a row, no further follow-up sampling was performed. These patients were excluded from the analysis because it hard to get reasonable fitting results. Also, we used 54 patients for the viral dynamics fitting and then only used the NFV cohort for clinical data analysis. We acknowledge that our description may have confused readers. We revised our manuscript to clarify these points regarding patient selecting for data fitting (page 6, lines 96-102, page 24, lines 406-407, and page 7, lines 410-412). In addition, we realized, thanks to the reviewer’s comment, that gender information was missing in Table 1. We appreciate this observation and have revised the table to include gender (we used gender in our analysis). 

(2) Exact study timeline for explanatory covariates: I understand the idea of finding « early predictors » of long-lasting viral shedding. I believe it is key and a great question. However, some samples (Figure 4A) seem to be taken at the end of the viral shedding. I am not sure it is really easier to micro-RNA saliva samples than a PCR. So I need to be better convinced of the impact of the possible findings. Generally, the timeline of explanatory covariate is not described in a satisfactory manner in the actual manuscript. Also, the evaluation and inclusion of the daily symptoms in the analysis are unclear to me.

We appreciate the reviewer’s feedback regarding the collection of explanatory variables. As noted, of the two microRNA samples collected from each patient, one was obtained near the end of viral shedding. This was intended to examine potential differences in microRNA levels between the early and late phases of infection. No significant differences were observed between the two time points, and using microRNA from either phase alone or both together did not substantially affect predictive accuracy for stratified groups. Furthermore, microRNA collection was motivated primarily by the expectation that it would be more sensitive to immune responses, rather than by ease of sampling. We have revised the manuscript to clarify these points regarding microRNA (page 17, lines 243-245 and 259-262).

Furthermore, as suggested by the reviewer, we have also strengthened the explanation regarding the collection schedule of clinical information and the use of daily symptoms in the analysis (page 6, lines 90-95, page 14, lines 218-220,).

(3) Early Trajectory Differentiation: The model struggles to differentiate between patients' viral load trajectories in the early phase, with overlapping slopes and indistinguishable viral load peaks observed in Figures 2B, 2C, and 2D. The question arises whether this issue stems from the data, the nature of Covid-19, or the model itself. The authors discuss the scarcity of pre-symptom data, primarily relying on Illinois patients who underwent testing before symptom onset. This contrasts earlier statements on pages 5-6 & 23, where they claim the data captures the full infection dynamics, suggesting sufficient early data for pre-symptom kinetics estimation. The authors need to provide detailed information on the number or timing of patient sample collections during each period.

Thank you for the reviewer’s thoughtful comments. The model used in this study [Eqs.(1-2)] has been employed in numerous prior studies and has successfully identified viral dynamics at the individual level. In this context, we interpret the rapid viral increase observed across participants as attributable to characteristics of SARS-CoV-2 in saliva, an interpretation that has also been reported by multiple previous studies. We have added the relevant references and strengthened the corresponding discussion in the manuscript (page 20, lines 303-311).

We acknowledge that our explanation of how the complementary relationship between the two cohorts contributes to capturing infection dynamics was not sufficiently clear. As described in the manuscript, the Illinois cohort provides pre-symptomatic data, whereas the NFV cohort offers abundant end-phase data, thereby compensating for each other’s missing phases. By jointly analyzing the two cohorts with a nonlinear mixed-effects model, we estimated viral dynamics at the individual-level. This approach first estimates population-level parameters (fixed effects) using data from all participants and then incorporates random effects to account for individual variability, yielding the most plausible parameter values.

Thus, even when early-phase data are lacking in the NFV cohort, information from the Illinois cohort allows us to infer most reasonable dynamics, and the reverse holds true for the end phase. In this context, we argued that combining the two cohorts enables mathematical modeling to capture infection dynamics at the individual level. Recognizing that our earlier description could be misleading, we have carefully reinforced the relevant description (page 27, lines 472-483). In addition, as suggested by the reviewer, we have added information on the number of data samples available for each phase in both cohorts (page 7, lines 106-109).

(4) Conditioning on the future: Conditioning on the future in statistics refers to the problematic situation where an analysis inadvertently relies on information that would not have been available at the time decisions were made or data were collected. This seems to be the case when the authors create micro-RNA data (Figure 4A). First, when the sampling times are is something that needs to be clarified by the authors (for clinical outcomes as well). Second, proper causal inference relies on the assumption that the cause precedes the effect. This conditioning on the future may result in overestimating the model's accuracy. This happens because the model has been exposed to the outcome it's supposed to predict. This could question the - already weak - relation with mir-1846 level.

We appreciate the reviewer’s detailed feedback. As noted in Reply to Comments 2, we collected micro-RNA samples at two time points, near the peak of infection dynamics and at the end stage, and found no significant differences between them. This suggests that micro-RNA levels are not substantially affected by sampling time. Indeed, analyses conducted using samples from the peak, late stage, or both yielded nearly identical results in relation to infection dynamics. To clarify this point, we revised the manuscript by integrating this explanation with our response in Reply to Comments 2 (page 17, lines 259-262). In addition, now we also revised manuscript to clarify sampling times of clinical information and micro-RNA (page 6, lines 90-95).

(5) Mathematical Model Choice Justification and Performance: The paper lacks mention of the practical identifiability of the model (especially for tau regarding the lack of early data information). Moreover, it is expected that the immune effector model will be more useful at the beginning of the infection (for which data are the more parsimonious). Please provide AIC for comparison, saying that they have "equal performance" is not enough. Can you provide at least in a point-by-point response the VPC & convergence assessments?

We appreciate the reviewer’s detailed feedback regarding the mathematical model. We acknowledge the potential concern regarding the practical identifiability of tau (incubation period), particularly given the limited early-phase data. In our analysis, however, the nonlinear mixed-effects model yielded a population-level estimate of 4.13 days, which is similar with previously reported incubation periods for COVID-19. This concordance suggests that our estimate of tau is reasonable despite the scarcity of early data.

For model comparison, first, we have added information on the AIC of the two models to the manuscript as suggested by the reviewer (page 10, lines 130-135). One point we would like to emphasize is that we adopted a simple target cell-limited model in this study, aiming to focus on reconstruction of viral dynamics and stratification of shedding patterns rather than exploring the mechanism of viral infection in detail. Nevertheless, we believe that the target cell-limited model provides reasonable reconstructed viral dynamics as it has been used in many previous studies. We revised manuscript to clarify this (page 10, lines 135-144). 

Furthermore, as suggested, we have added the VPC and convergence assessment results for both models, together with explanatory text, to the manuscript (Supplementary Fig 2, Supplementary Fig 3, and page 10, lines 130-135). In the VPC, the observed 5th, 50th, and 95th percentiles were generally within the corresponding simulated prediction intervals across most time points. Although minor deviations were noted in certain intervals, the overall distribution of the observed data was well captured by the models, supporting their predictive performance (Supplementary Fig 2). In addition, the log-likelihood and SAEM parameter trajectories stabilized after the burn-in phase, confirming appropriate convergence (Supplementary Fig 3).

(6) Selected features of viral shedding: I wonder to what extent the viral shedding area under the curve (AUC) and normalized AUC should be added as selected features.

We sincerely appreciate the reviewer’s valuable suggestion regarding the inclusion of additional features. Following this recommendation, we considered AUC (or normalized AUC) as an additional feature when constructing the distance matrix used for stratification. We then evaluated the similarity between the resulting distance matrix and the original one using the Mantel test, which showed a very high correlation (r = 0.92, p < 0.001). This indicates that incorporating AUC as an additional feature does not substantially alter the distance matrix. Accordingly, we have decided to retain the current stratification analysis, and we sincerely thank the reviewer once again for this interesting suggestion.

(7) Two-step nature of the analysis: First you fit a mechanistic model, then you use the predictions of this model to perform clustering and prediction of groups (unsupervised then supervised). Thus you do not propagate the uncertainty intrinsic to your first estimation through the second step, ie. all the viral load selected features actually have a confidence bound which is ignored. Did you consider a one-step analysis in which your covariates of interest play a direct role in the parameters of the mechanistic model as covariates? To pursue this type of analysis SCM (Johnson et al. Pharm. Res. 1998), COSSAC (Ayral et al. 2021 CPT PsP), or SAMBA ( Prague et al. CPT PsP 2021) methods can be used. Did you consider sampling on the posterior distribution rather than using EBE to avoid shrinkage?

Thank you for the reviewer’s detailed suggestions regarding our analysis. We agree that the current approach does not adequately account for the impact of uncertainty in viral dynamics on the stratified analyses. As a first step, we have revised Extended Data Fig 1 (now renumbered as Supplementary Fig 1) to include 95% credible intervals computed using a bootstrap approach, to present the model-fitting uncertainty more explicitly. Then, to examine the potential impact of model uncertainty on stratified analyses, we reconstructed the distance matrix underlying stratification by incorporating feature uncertainty. Specifically, for each individual, we sampled viral dynamics within the credible interval and averaged the resulting feature, and build the distance matrix using it. We then compared this uncertainty-adjusted matrix with the original one using the Mantel test, which showed a strong correlation (r = 0.72, p < 0.001). Given this result, we did not replace the current stratification but revised the manuscript to provide this information (page 11, lines 159-162 and page 28, 512-519).

Furthermore, we carefully considered the reviewer’s proposed one-step analysis. However, implementation was constrained by data-fitting limitations. Concretely, clinical information is available only in the NFV cohort. Thus, if these variables are to be entered directly as covariates on the parameters, the Illinois cohort cannot be included in the data-fitting process. Yet the NFV cohort lacks any pre-symptomatic observations, so fitting the model to that cohort alone does not permit a reasonable (well-identified/robust) fitting result. While we were unable to implement the suggestion under the current data constraints, we sincerely appreciate the reviewer’s thoughtful and stimulating proposal.

(8) Need for advanced statistical methods: The analysis is characterized by a lack of power. This can indeed come from the sample size that is characterized by the number of data available in the study. However, I believe the power could be increased using more advanced statistical methods. At least it is worth a try. First considering the unsupervised clustering, summarizing the viral shedding trajectories with features collapses longitudinal information. I wonder if the R package « LongituRF » (and associated method) could help, see Capitaine et al. 2020 SMMR. Another interesting tool to investigate could be latent class models R package « lcmm » (and associated method), see ProustLima et al. 2017 J. Stat. Softwares. But the latter may be more far-reached.

Thank you for the reviewer’s thoughtful suggestions regarding our unsupervised clustering approach. The R package “LongitiRF” is designed for supervised analysis, requiring a target outcome to guide the calculation of distances between individuals (i.e., between viral dynamics). In our study, however, the goal was purely unsupervised clustering, without any outcome variable, making direct application of “LongitiRF” challenging.

Our current approach (summarizing each dynamic into several interpretable features and then using Random Forest proximities) allows us to construct a distance matrix in an unsupervised manner. Here, the Random Forest is applied in “proximity mode,” focusing on how often dynamics are grouped together in the trees, independent of any target variable. This provides a practical and principled way to capture overall patterns of dynamics while keeping the analysis fully unsupervised.

Regarding the suggestion to use latent class mixed models (R package “lcmm”), we also considered this approach. In our dataset, each subject has dense longitudinal measurements, and at many time points, trajectories are very similar across subjects, resulting in minimal inter-individual differences. Consequently, fitting multi-class latent class mixed models (ng ≥ 2) with random effects or mixture terms is numerically unstable, often producing errors such as non-positive definite covariance matrices or failure to generate valid initial values. Although one could consider using only the time points with the largest differences, this effectively reduces the analysis to a feature-based summary of dynamics. Such an approach closely resembles our current method and contradicts the goal of clustering based on full longitudinal information.

Taken together, although we acknowledge that incorporating more longitudinal information is important, we believe that our current approach provides a practical, stable, and informative solution for capturing heterogeneity in viral dynamics. We would like to once again express our sincere gratitude to the reviewer for this insightful suggestion.

(9) Study intrinsic limitation: All the results cannot be extended to asymptomatic patients and patients infected with recent VOCs. It definitively limits the impact of results and their applicability to public health. However, for me, the novelty of the data analysis techniques used should also be taken into consideration.

We appreciate your positive evaluation of our research approach and acknowledge that, as noted in the Discussion section as our first limitation, our analysis may not provide valid insights into recent VOCs or all populations, including asymptomatic individuals. Nonetheless, we believe it is novel that we extensively investigated the relationship between viral shedding patterns in saliva and a wide range of clinical and micro-RNA data. Our findings contribute to a deeper and more quantitative understanding of heterogeneity in viral dynamics, particularly in saliva samples. To discuss this point, we revised our manuscript (page 22, lines 364-368).

Strengths are:

Unique data and comprehensive analysis.

Novel results on viral shedding.

Weaknesses are:

Limitation of study design.

The need for advanced statistical methodology.

Reviewer #1 (Recommendations For The Authors):

Line 8: In the abstract, it would be helpful to state how stratification occurred.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 2, lines 8-11).

Line 31 and discussion: It is important to mention the challenges of using saliva as a specimen type for lab personnel.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 36-41).

Line 35: change to "upper respiratory tract".

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, line 35).

Line 37: "Saliva" is not a tissue. Please hazard a guess as to which tissue is responsible for saliva shedding and if it overlaps with oral and nasal swabs.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 42-45).

Line 42, 68: Please explain how understanding saliva shedding dynamics would impact isolation & screening, diagnostics, and treatments. This is not immediately intuitive to me.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 48-50).

Line 50: It would be helpful to explain why shedding duration is the best stratification variable.

We thank the reviewer for the feedback. We acknowledge that our wording was ambiguous. The clear differences in the viral dynamics patterns pertain to findings observed following the stratification, and we have revised the manuscript to make this explicit (page 4, lines 59-61).

Line 71: Dates should be listed for these studies.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 6, lines 85-86).

Reviewer #2 (Recommendations For The Authors):

Please make all code and data available for replication of the analyses.

We appreciate the suggestion. Due to ethical considerations, it is not possible to make all data and code publicly available. We have clearly stated in the manuscript about it (Data availability section in Methods).

Reviewer #3 (Recommendations For The Authors):

Here are minor comments / technical details:

(1) Figure 1B is difficult to understand.

Thank you for the comment. We updated Fig 1B to incorporate more information to aid interpretation.

(2) Did you analyse viral load or the log10 of viral load? The latter is more common. You should consider it. SI Figure 1 please plot in log10 and use a different point shape for censored data. The file quality of this figure should be improved. State in the material and methods if SE with moonlit are computed with linearization or importance sampling.

Thank you for the comment. We conducted our analyses using log10-transformed viral load. Also, we revised Supplementary Fig 1 (now renumbered as Supplementary Fig 4) as suggested. We also added Supplementary Fig 3 and clarified in the Methods that standard errors (SE) were obtained in Monolix from the Fisher information matrix using the linearization method (page 28, lines 498-499).

(3) Table 1 and Figure 3A could be collapsed.

Thank you for the comment, and we carefully considered this suggestion. Table 1 summarizes clinical variables by category, whereas Fig 3A visualizes them ordered by p-value of statistical analysis. Collapsing these into a single table would make it difficult to apprehend both the categorical summaries and the statistical ranking at a glance, thereby reducing readability. We therefore decided to retain the current layout. We appreciate the constructive feedback again. 

(4) Figure 3 legend could be clarified to understand what is 3B and 3C.

We thank the reviewer for the feedback and have reinforced the description accordingly.

(5) Why use AIC instead of BICc?

Thank you for your comment. We also think BICc is a reasonable alternative. However, because our objective is predictive adequacy (reconstruction of viral dynamics), we judged AIC more appropriate. In NLMEM settings, the effective sample size required by BICc is ambiguous, making the penalty somewhat arbitrary. Moreover, since the two models reconstruct very similar dynamics, our conclusions are not sensitive to the choice of criterion.

(6) Bibliography. Most articles are with et al. (which is not standard) and some are with an extended list of names. Provide DOI for all.

We thank the reviewer for the feedback, and have revised the manuscript accordingly.

(7) Extended Table 1&2 - maybe provide a color code to better highlight some lower p-values (if you find any interesting).

We thank the reviewer for the feedback. Since no clinical information and micro-RNAs other than mir-1846 showed low p-values, we highlighted only mir-1846 with color to make it easier to locate.

(8) Please make the replication code available.

We appreciate the suggestion. Due to ethical considerations, it is not possible to make all data and code publicly available. We have clearly stated in the manuscript about it (Data availability section in Methods).

eLife Assessment

The findings of this study are valuable as it demonstrates that when treatment is initiated during acute infection, HIV specific CD8 T cell responses are maintained long term and continued proliferative capacity of these cells may play a role in reducing HIV DNA levels. The evidence supporting the conclusions are solid with rigorous and advanced methodology used with the major limitations being that the findings are association level and do not meet strict criteria for causality. The work is of interest to the HIV cure field and suggests that enhancing early HIV specific CD8 T cell responses should be considered in the design of interventional cure strategies.

Reviewer #2 (Public review):

This study investigated the impact of early HIV specific CD8 T cell responses on the viral reservoir size after 24 weeks and 3 years of follow up in individuals who started ART during acute infection. Viral reservoir quantification showed that total and defective HIV DNA, but not intact, declined significantly between 24 weeks and 3 years post-ART. The authors also showed that functional HIV-specific CD8⁺ T-cell responses persisted over three years and that early CD8⁺ T-cell proliferative capacity was linked to reservoir decline, supporting early immune intervention in the design of curative strategies.

The paper is well written, easy to read, and the findings are clearly presented. The study is novel as it demonstrates the effect of HIV specific CD8 T cell responses on different states of the HIV reservoir, that is HIV-DNA (intact and defective), the transcriptionally active and inducible reservoir. Although small, the study cohort was relevant and well-characterized as it included individuals who initiated ART during acute infection, 12 of whom were followed longitudinally for 3 years, providing unique insights into the beneficial effects of early treatment on both immune responses and the viral reservoir. The study uses advanced methodology. I enjoyed reading the paper.

The study's limitations are minor and well acknowledged. While the cohort included only male participants-potentially limiting generalizability-the authors have clarified this limitation in the discussion. Although a chronic infection control group was not yet available, the authors explained that their protocol includes plans to add this comparison in future studies. These limitations are appropriately addressed and do not undermine the strength or validity of the study's conclusions.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

In this work, van Paassen et al. have studied how CD8 T cell functionality and levels predict HIV DNA decline. The article touches on interesting facets of HIV DNA decay, but ultimately comes across as somewhat hastily done and not convincing due to the major issues. 

(1) The use of only 2 time points to make many claims about longitudinal dynamics is not convincing. For instance, the fact that raw data do not show decay in intact, but do for defective/total, suggests that the present data is underpowered. The authors speculate that rising intact levels could be due to patients who have reservoirs with many proviruses with survival advantages, but this is not the parsimonious explanation vs the data simply being noisy without sufficient longitudinal follow-up. n=12 is fine, or even reasonably good for HIV reservoir studies, but to mitigate these issues would likely require more time points measured per person. 

(1b) Relatedly, the timing of the first time point (6 months) could be causing a number of issues because this is in the ballpark for when the HIV DNA decay decelerates, as shown by many papers. This unfortunate study design means some of these participants may already have stabilized HIV DNA levels, so earlier measurements would help to observe early kinetics, but also later measurements would be critical to be confident about stability. 

The main goal of the present study was to understand the relationship of the HIV-specific CD8 T-cell responses early on ART with the reservoir changes across the subsequent 2.5-year period on suppressive therapy. We have revised the manuscript in order to clarify this.  We chose these time points because the 24 week time point is past the initial steep decline of HIV DNA, which takes place in the first weeks after ART initiation. It is known that HIV DNA continues to decay for years after (Besson, Lalama et al. 2014, Gandhi, McMahon et al. 2017). 

(2) Statistical analysis is frequently not sufficient for the claims being made, such that overinterpretation of the data is problematic in many places. 

(2a) First, though plausible that cd8s influence reservoir decay, much more rigorous statistical analysis would be needed to assert this directionality; this is an association, which could just as well be inverted (reservoir disappearance drives CD8 T cell disappearance). 

To correlate different reservoir measures between themselves and with CD8+ T-cell responses at 24 and 156 weeks, we now performed non-parametric (Spearman) correlation analyses, as they do not require any assumptions about the normal distribution of the independent and dependent variables. Benjamini-Hochberg corrections for multiple comparisons (false discovery rate, 0.25) were included in the analyses and did not change the results. 

Following this comment we would like to note that the association between the T-cell response at 24 weeks and the subsequent decrease in the reservoir cannot be bi-directional (that can only be the case when both variables are measured at the same time point). Therefore, to model the predictive value of T-cell responses measured at 24 weeks for the decrease in the reservoir between 24 and 156 weeks, we fitted generalized linear models (GLM), in which we included age and ART regimen, in addition to three different measures of HIV-specific CD8+ T-cell responses, as explanatory variables, and changes in total, intact, and total defective HIV DNA between 24 and 156 weeks ART as dependent variables.

(2b) Words like "strong" for correlations must be justified by correlation coefficients, and these heat maps indicate many comparisons were made, such that p-values must be corrected appropriately. 

We have now used Spearman correlation analysis, provided correlation coefficients to justify the wording, and adjusted the p-values for multiple comparisons (Fig. 1, Fig 3., Table 2). Benjamini-Hochberg corrections for multiple comparisons (false discovery rate, 0.25) were included in the analyses and did not change the results.  

(3) There is not enough introduction and references to put this work in the context of a large/mature field. The impacts of CD8s in HIV acute infection and HIV reservoirs are both deep fields with a lot of complexity. 

Following this comment we have revised and expanded the introduction to put our work more in the context of the field (CD8s in acute HIV and HIV reservoirs). 

Reviewer #2 (Public review): 

Summary: 

This study investigated the impact of early HIV specific CD8 T cell responses on the viral reservoir size after 24 weeks and 3 years of follow-up in individuals who started ART during acute infection. Viral reservoir quantification showed that total and defective HIV DNA, but not intact, declined significantly between 24 weeks and 3 years post-ART. The authors also showed that functional HIV-specific CD8⁺ T-cell responses persisted over three years and that early CD8⁺ T-cell proliferative capacity was linked to reservoir decline, supporting early immune intervention in the design of curative strategies. 

Strengths: 

The paper is well written, easy to read, and the findings are clearly presented. The study is novel as it demonstrates the effect of HIV specific CD8 T cell responses on different states of the HIV reservoir, that is HIV-DNA (intact and defective), the transcriptionally active and inducible reservoir. Although small, the study cohort was relevant and well-characterized as it included individuals who initiated ART during acute infection, 12 of whom were followed longitudinally for 3 years, providing unique insights into the beneficial effects of early treatment on both immune responses and the viral reservoir. The study uses advanced methodology. I enjoyed reading the paper. 

Weaknesses: 

All participants were male (acknowledged by the authors), potentially reducing the generalizability of the findings to broader populations. A control group receiving ART during chronic infection would have been an interesting comparison. 

We thank the reviewer for their appreciation of our study. Although we had indeed acknowledged the fact that all participants were male, we have clarified why this is a limitation of the study (Discussion, lines 296-298). The reviewer raises the point that it would be useful to compare our data to a control group. Unfortunately, these samples are not yet available, but our study protocol allows for a control group (chronic infection) to ensure we can include a control group in the future.

Reviewer #1 (Recommendations for the authors): 

Minor: 

On the introduction: 

(1) One large topic that is mostly missing completely is the emerging evidence of selection on HIV proviruses during ART from the groups of Xu Yu and Matthias Lichterfeld, and Ya Chi Ho, among others. 

Previously, it was only touched upon in the Discussion. Now we have also included this in the Introduction (lines 77-80).

(2) References 4 and 5 don't quite match with the statement here about reservoir seeding; we don't completely understand this process, and certainly, the tissue seeding aspect is not known. 

Line 61-62: references were changed and this paragraph was rewritten to clarify.

(3) Shelton et al. showed a strong relationship with HIV DNA size and timing of ART initiation across many studies. I believe Ananwaronich also has several key papers on this topic. 

References by Ananwaronich are included (lines 91-94).

(4) "the viral levels decline within weeks of AHI", this is imprecise, there is a peak and a decline, and an equilibrium. 

We agree and have rewritten the paragraph accordingly.

(5) The impact of CD8 cells on viral evolution during primary infection is complex and likely not relevant for this paper. 

We have left viral evolution out of the introduction in order to keep a focus on the current subject.

(6) The term "reservoir" is somewhat polarizing, so it might be worth mentioning somewhere exactly what you think the reservoir is, I think, as written, your definition is any HIV DNA in a person on ART? 

Indeed, we refer to the reservoir when we talk about the several aspects of the reservoir that we have quantified with our assays (total HIV DNA, unspliced RNA, intact and defective proviral DNA, and replication-competent virus). In most instances we try to specify which measurement we are referring to. We have added additional reservoir explanation to clarify our definition to the introduction (lines 55-58).

(7) I think US might be used before it is defined. 

We thank the reviewer for this notification, we have now also defined it in the Results section (line 131).

(8) In Figure 1 it's also not clear how statistics were done to deal with undetectable values, which can be tricky but important. 

We have now clarified this in the legend to Figure 2 (former Figure 1). Paired Wilcoxon tests were performed to test the significance of the differences between the time points. Pairs where both values were undetectable were always excluded from the analysis. Pairs where one value was undetectable and its detection limit was higher than the value of the detectable partner, were also excluded from the analysis. Pairs where one value was undetectable and its detection limit was lower than the value of the detectable partner, were retained in the analysis.

In the discussion: 

(1) "This confirms that the existence of a replication-competent viral reservoir is linked to the presence of intact HIV DNA." I think this statement is indicative of many of the overinterpretations without statistical justification. There are 4 of 12 individuals with QVOA+ detectable proviruses, which means there are 8 without. What are their intact HIV DNA levels? 

We thank the reviewer for the question that is raised here. We have now compared the intact DNA levels (measured by IPDA) between participants with positive vs. negative QVOA output, and observed a significant difference. We rephrased the wording as follows: “We compared the intact HIV DNA levels at the 24-week timepoint between the six participants, from whom we were able to isolate replicating virus, and the fourteen participants, from whom we could not. Participants with positive QVOA had significantly higher intact HIV DNA levels than those with negative QVOA (p=0.029, Mann-Whitney test; Suppl. Fig. 3). Five of six participants with positive QVOA had intact DNA levels above 100 copies/106 PBMC, while thirteen of fourteen participants with negative QVOA had intact HIV DNA below 100 copies/106 PBMC (p=0.0022, Fisher’s exact test). These findings indicate that recovery of replication-competent virus by QVOA is more likely in individuals with higher levels of intact HIV DNA in IPDA, reaffirming a link between the two measurements.”

(2) "To determine whether early HIV-specific CD8+ T-cell responses at 24 weeks were predictive for the change in reservoir size". This is a fundamental miss on correlation vs causation... it could be the inverse. 

We thank the reviewer for the remark. We have calculated the change in reservoir size (the difference between the reservoir size at 24 weeks and 156 weeks ART) and analyzed if the HIVspecific CD8+ T-cell response at 24 weeks ART are predictive for this change. We do not think it can be inverse, as we have a chronological relationship (CD8+ responses at week 24 predict the subsequent change in the reservoir).

(3) "This may suggest that active viral replication drives the CD8+ T-cell response." I think to be precise, you mean viral transcription drives CD8s, we don't know about the full replication cycle from these data. 

We agree with the reviewer and have changed “replication” to “transcription” (line 280).

(4) "Remarkably, we observed that the defective HIV DNA levels declined significantly between 24 weeks and 3 years on ART. This is in contrast to previous observations in chronic HIV infection (30)". I don't find this remarkable or in contrast: many studies have analyzed and/or modeled defective HIV DNA decay, most of which have shown some negative slope to defective HIV DNA, especially within the first year of ART. See White et al., Blankson et al., Golob et al., Besson et al., etc In addition, do you mean in long-term suppressed? 

The point we would like to make is that,  compared to other studies, we found a significant, prominent decrease in defective DNA (and not intact DNA) over the course of 3 years, which is in contrast to other studies (where usually the decrease in intact is significant and the decrease in defective less prominent). We have rephrased the wording (lines 227-230) as follows:

“We observed that the defective HIV DNA levels decreased significantly between 24 and 156 weeks of ART. This is different from studies in CHI, where no significant decrease during the first 7 years of ART (Peluso, Bacchetti et al. 2020, Gandhi, Cyktor et al. 2021), or only a significant decrease during the first 8 weeks on ART, but not in the 8 years thereafter, was observed (Nühn, Bosman et al. 2025).”

Reviewer #2 (Recommendations for the authors): 

(1) Page 4, paragraph 2 - will be informative to report the statistics here. 

(2) Page 4, paragraph 4 - "General phenotyping of CD4+ (Suppl. Fig. 3A) and CD8+ (Supplementary Figure 3B) T-cells showed no difference in frequencies of naïve, memory or effector CD8+ T-cells between 24 and 156 weeks." - What did the CD4+ phenotyping show? 

We thank the reviewer for the remark. Indeed, there were also no differences in frequencies of naïve, memory or effector CD4+ T-cells between 24 and 156 weeks. We have added this to the paragraph (now Suppl. Fig 4), lines 166-168.

(3) Page 5, paragraph 3 - "Similarly, a broad HIV-specific CD8+ T-cell proliferative response to at least three different viral proteins was observed in the majority of individuals at both time points" - should specify n=? for the majority of individuals. 

At time point 24 weeks, 6/11 individuals had a response to env, 10/11 to gag, 5/11 to nef, and 4/11 to pol. At 156 weeks, 8/11 to env, 10/11 to gag, 8/11 to nef and 9/11 to pol. We have added this to the text (lines 188-191).

(4) Seven of 22 participants had non-subtype B infection. Can the authors explain the use of the IPDA designed by Bruner et. al. for subtype B HIV, and how this may have affected the quantification in these participants? 

Intact HIV DNA was detectable in all 22 participants. We cannot completely exclude influence of primer/probe-template mismatches on the quantification results, however such mismatches could also have occurred in subtype B participants, and droplet digital PCR that IPDA is based on is generally much less sensitive to these mismatches than qPCR.

(5) Page 7, paragraph 2 - the authors report a difference in findings from a previous study ("a decline in CD8 T cell responses over 2 years" - reference 21), but only provide an explanation for this on page 9. The authors should consider moving the explanation to this paragraph for easier understanding. 

We agree with the reviewer that this causes confusion. Therefore, we have revised and changed the order in the Discussion.

(6) Page 7, paragraph 2 - Following from above, the previous study (21) reported this contradicting finding "a decline in CD8 T cell responses over 2 years" in a CHI (chronic HIV) treated cohort. The current study was in an acute HIV treated cohort. The authors should explain whether this may also have resulted in the different findings, in addition to the use of different readouts in each study.

We thank the reviewer for this attentiveness. Indeed, the study by Takata et al. investigates the reservoir and HIV-specific CD8+ T-cell responses in both the RV254/ SEARCH010 study who initiated ART during AHI and the RV304/ SEARCH013 who initiated ART during CHI. We had not realized that the findings of the decline in CD8 T cell responses were solely found in the RV304/ SEARCH013 (CHI cohort). It appears functional HIV specific immune responses were only measured in AHI at 96 weeks, so we have clarified this in the Discussion. 

Besson, G. J., C. M. Lalama, R. J. Bosch, R. T. Gandhi, M. A. Bedison, E. Aga, S. A. Riddler, D. K. McMahon, F. Hong and J. W. Mellors (2014). "HIV-1 DNA decay dynamics in blood during more than a decade of suppressive antiretroviral therapy." Clin Infect Dis 59(9): 1312-1321.

Gandhi, R. T., J. C. Cyktor, R. J. Bosch, H. Mar, G. M. Laird, A. Martin, A. C. Collier, S. A. Riddler, B. J. Macatangay, C. R. Rinaldo, J. J. Eron, J. D. Siliciano, D. K. McMahon and J. W. Mellors (2021). "Selective Decay of Intact HIV-1 Proviral DNA on Antiretroviral Therapy." J Infect Dis 223(2): 225-233.

Gandhi, R. T., D. K. McMahon, R. J. Bosch, C. M. Lalama, J. C. Cyktor, B. J. Macatangay, C. R. Rinaldo, S. A. Riddler, E. Hogg, C. Godfrey, A. C. Collier, J. J. Eron and J. W. Mellors (2017). "Levels of HIV-1 persistence on antiretroviral therapy are not associated with markers of inflammation or activation." PLoS Pathog 13(4): e1006285.

Nühn, M. M., K. Bosman, T. Huisman, W. H. A. Staring, L. Gharu, D. De Jong, T. M. De Kort, N. Buchholtz, K. Tesselaar, A. Pandit, J. Arends, S. A. Otto, E. Lucio De Esesarte, A. I. M. Hoepelman, R. J. De Boer, J. Symons, J. A. M. Borghans, A. M. J. Wensing and M. Nijhuis (2025). "Selective decline of intact HIV reservoirs during the first decade of ART followed by stabilization in memory T cell subsets." Aids 39(7): 798-811.

Peluso, M. J., P. Bacchetti, K. D. Ritter, S. Beg, J. Lai, J. N. Martin, P. W. Hunt, T. J. Henrich, J. D. Siliciano, R. F. Siliciano, G. M. Laird and S. G. Deeks (2020). "Differential decay of intact and defective proviral DNA in HIV-1-infected individuals on suppressive antiretroviral therapy." JCI Insight 5(4).

eLife Assessment

This manuscript provides evidence that mouse germline cysts develop an asymmetric Golgi, ER, and microtubule-associated structure, referred to as Visham, which in many ways resembles the fusome of Drosophila germline cysts. This is an important study that provides new evidence that fusome-like structures exist in germ cell cysts across species. While most of the data are solid, several instances remain in which conclusions regarding the dynamics and function of Visham should be restated, or additional experimental evidence should be provided to more fully support the authors' interpretations.

Reviewer #1 (Public review):

Summary:

The authors attempt to study how oocyte incomplete cytokinesis occurs in the mouse ovary.

Strengths:

The finding that UPR components are highly expressed during zygotene is an interesting result that has broad implications for how germ cells navigate meiosis. The findings that proteasome activity increases in germ cells compared to somatic cells suggest that the germline might have a quantitatively different response for protein clearance.

Weaknesses:

(1) The microscopy images look saturated, for example, Figure 1a, b, etc? Is this a normal way to present fluorescent microscopy?

(2) The authors should ensure that all claims regarding enrichment/lower vs lower values have indicated statistical tests.

(a) In Figure 2f, the authors should indicate which comparison is made for this test. Is it comparing 2 vs 6 cyst numbers?

(b) Figures 4d and 4e do not have a statistical test indicated.

(3) Because the system is developmentally dynamic, the major conclusions of the work are somewhat unclear. Could the authors be more explicit about these and enumerate them more clearly in the abstract?

(4) The references for specific prior literature are mostly missing (lines 184-195, for example).

(5) The authors should define all acronyms when they are first used in the text (UPR, EGAD, etc).

(6) The jumping between topics (EMA, into microtubule fragmentation, polarization proteins, UPR/ERAD/EGAD, GCNA, ER, balbiani body, etc) makes the narrative of the paper very difficult to follow.

(7) The heading title "Visham participates in organelle rejuvenation during meiosis" in line 241 is speculative and/or not supported. Drawing upon the extensive, highly rigorous Drosophila literature, it is safe to extrapolate, but the claim about regeneration is not adequately supported.

Reviewer #2 (Public review):

This study identifies Visham, an asymmetric structure in developing mouse cysts resembling the Drosophila fusome, an organelle crucial for oocyte determination. Using immunofluorescence, electron microscopy, 3D reconstruction, and lineage labeling, the authors show that primordial germ cells (PGCs) and cysts, but not somatic cells, contain an EMA-rich, branching structure that they named Visham, which remains unbranched in male cysts. Visham accumulates in regions enriched in intercellular bridges, forming clusters reminiscent of fusome "rosettes." It is enriched in Golgi and endosomal vesicles and partially overlaps with the ER. During cell division, Visham localizes near centrosomes in interphase and early metaphase, disperses during metaphase, and reassembles at spindle poles during telophase before becoming asymmetric. Microtubule depolymerization disrupts its formation.

Cyst fragmentation is shown to be non-random, correlating with microtubule gaps. The authors propose that 8-cell (or larger) cysts fragment into 6-cell and 2-cell cysts. Analysis of Pard3 (the mouse ortholog of Par3/Baz) reveals its colocalization with Visham during cyst asymmetry, suggesting that mammalian oocyte polarization depends on a conserved system involving Par genes, cyst formation, and a fusome-like structure.

Transcriptomic profiling identifies genes linked to pluripotency and the unfolded protein response (UPR) during cyst formation and meiosis, supported by protein-level reporters monitoring Xbp1 splicing and 20S proteasome activity. Visham persists in meiotic germ cells at stage E17.5 and is later transferred to the oocyte at E18.5 along with mitochondria and Golgi vesicles, implicating it in organelle rejuvenation. In Dazl mutants, cysts form, but Visham dynamics, polarity, rejuvenation, and oocyte production are disrupted, highlighting its potential role in germ cell development.

Overall, this is an interesting and comprehensive study of a conserved structure in the germline cells of both invertebrate and vertebrate species. Investigating these early stages of germ cell development in mice is particularly challenging. Although primarily descriptive, the study represents a remarkable technical achievement. The images are generally convincing, with only a few exceptions.

Major comments:

(1) Some titles contain strong terms that do not fully match the conclusions of the corresponding sections.

(1a) Article title "Mouse germline cysts contain a fusome-like structure that mediates oocyte development":

The term "mediates" could be misleading, as the functional data on Visham (based on comparing its absence to wild-type) actually reflects either a microtubule defect or a Dazl mutant context. There is no specific loss-of-function of visham only.

(1b) Result title, "Visham overlaps centrosomes and moves on microtubules":

The term "moves" implies dynamic behavior, which would require live imaging data that are not described in the article.

(1c) Result title, "Visham associates with Golgi genes involved in UPR beginning at the onset of cyst formation":

The presented data show that the presence of Visham in the cyst coincides temporally with the expression and activity of the UPR response; the term "associates" is unclear in this context.

(1d) Result title, "Visham participates in organelle rejuvenation during meiosis":

The term "participates" suggests that Visham is required for this process, whereas the conclusion is actually drawn from the Dazl mutant context, not a specific loss-of-function of visham only.

(2) The authors aim to demonstrate that Visham is a fusome-like structure. I would suggest simply referring to it as a "fusome-like structure" rather than introducing a new term, which may confuse readers and does not necessarily help the authors' goal of showing the conservation of this structure in Drosophila and Xenopus germ cells. Interestingly, in a preprint from the same laboratory describing a similar structure in Xenopus germ cells, the authors refer to it as a "fusome-like structure (FLS)" (Davidian and Spradling, BioRxiv, 2025).

Reviewer #3 (Public review):

This manuscript provides evidence that mice have a fusome, a conserved structure most well studied in Drosophila that is important for oocyte specification. Overall, a myriad of evidence is presented demonstrating the existence of a mouse fusome that the authors term visham. This work is important as it addresses a long-standing question in the field of whether mice have fusomes and sheds light on how oocytes are specified in mammals. Concerns that need to be addressed revolve around several conclusions that are overstated or unclear and are listed below.

(1) Line 86 - the heading for this section is "PGCs contain a Golgi-rich structure known as the EMA granule" but there is nothing in this section that shows it is Golgi-rich. It does show that the structure is asymmetric and has branches.

(2) Line 105-106, how do we know if what's seen by EM corresponds to the EMA1 granule?

(3) Line 106-107-states "Visham co-stained with the Golgi protein Gm130 and the recycling endosomal protein Rab11a1". This is not convincing as there is only one example of each image, and both appear to be distorted.

(4) Line 132-133---while visham formation is disrupted when microtubules are disrupted, I am not convinced that visham moves on microtubules as stated in the heading of this section.

(5) Line 156 - the heading for this section states that Visham associates with polarity and microtubule genes, including pard3, but only evidence for pard3 is presented.

(6) Lines 196-210 - it's strange to say that UPR genes depend on DAZ, as they are upregulated in the mutants. I think there are important observations here, but it's unclear what is being concluded.

(7) Line 257-259---wave 1 and 2 follicles need to be explained in the introduction, and how this fits with the observations here clarified.

Author response:

Reviewer #1 (Public Review):

Summary

We thank the reviewer for the constructive and thoughtful evaluation of our work. We appreciate the recognition of the novelty and potential implications of our findings regarding UPR activation and proteasome activity in germ cells.

(1) The microscopy images look saturated, for example, Figure 1a, b, etc. Is this a normal way to present fluorescent microscopy?

The apparent saturation was not present in the original images, but likely arose from image compression during PDF generation. While the EMA granule was still apparent, in the revised submission, we will provide high-resolution TIFF files to ensure accurate representation of fluorescence intensity and will carefully optimize image display settings to avoid any saturation artifacts.

(2) The authors should ensure that all claims regarding enrichment/lower vs. lower values have indicated statistical tests.

We fully agree. In the revised version, we will correct any quantitative comparisons where statistical tests were not already indicated, with a clear statement of the statistical tests used, including p-values in figure legends and text.

(a) In Figure 2f, the authors should indicate which comparison is made for this test. Is it comparing 2 vs. 6 cyst numbers?

We acknowledge that the description was not sufficiently detailed. Indeed, the test was not between 2 vs 6 cyst numbers, but between all possible ways 8-cell cysts or the larger cysts studied could fragment randomly into two pieces, and produce by chance 6-cell cysts in 13 of 15 observed examples. We will expand the legend and main text to clarify that a binomial test was used to determine that the proportion of cysts producing 6-cell fragments differed very significantly from chance.

Revised text:

“A binomial test was used to assess whether the observed frequency of 6-cell cyst products differed from random cyst breakage. Production of 6-cell cysts was strongly preferred (13/15 cysts; ****p < 0.0001).”

(b) Figures 4d and 4e do not have a statistical test indicated.

We will include the specific statistical test used and report the corresponding p-values directly in the figure legends.

(3) Because the system is developmentally dynamic, the major conclusions of the work are somewhat unclear. Could the authors be more explicit about these and enumerate them more clearly in the abstract?

We will revise the abstract to better clarify the findings of this study. We will also replace the term Visham with mouse fusome to reflect its functional and structural analogy to the Drosophila and Xenopus fusomes, making the narrative more coherent and conclusive.

(4) The references for specific prior literature are mostly missing (lines 184-195, for example).

We appreciate this observation of a problem that occurred inadvertently when shortening an earlier version.  We will add 3–4 relevant references to appropriately support this section.

(5) The authors should define all acronyms when they are first used in the text (UPR, EGAD, etc).

We will ensure that all acronyms are spelled out at first mention (e.g., Unfolded Protein Response (UPR), Endosome and Golgi-Associated Degradation (EGAD)).

(6)  The jumping between topics (EMA, into microtubule fragmentation, polarization proteins, UPR/ERAD/EGAD, GCNA, ER, balbiani body, etc) makes the narrative of the paper very difficult to follow.

We are not jumping between topics, but following a narrative relevant to the central question of whether female mouse germ cells develop using a fusome.  EMA, microtubule fragmentation, polarization proteins, ER, and balbiani body are all topics with a known connection to fusomes. This is explained in the general introduction and in relevant subsections. We appreciate this feedback that further explanations of these connections would be helpful. In the revised manuscript, use of the unified term mouse fusome will also help connect the narrative across sections.  UPR/ERAD/EGAD are processes that have been studied in repair and maintenance of somatic cells and in yeast meiosis.  We show that the major regulator XbpI is found in the fusome, and that the fusome and these rejuvenation pathway genes are expressed and maintained throughout oogenesis, rather than only during limited late stages as suggested in previous literature.

(7) The heading title "Visham participates in organelle rejuvenation during meiosis" in line 241 is speculative and/or not supported. Drawing upon the extensive, highly rigorous Drosophila literature, it is safe to extrapolate, but the claim about regeneration is not adequately supported.

We believe this statement is accurate given the broad scope of the term "participates." It is supported by localization of the UPR regulator XbpI to the fusome. XbpI is the ortholog of HacI a key gene mediating UPR-mediated rejuvenation during yeast meiosis.  We also showed that rejuvenation pathway genes are expressed throughout most of meiosis (not previously known) and expanded cytological evidence of stage-specific organelle rejuvenation later in meiosis, such as mitochondrial-ER docking, in regions enriched in fusome antigens. However, we recognize the current limitations of this evidence in the mouse, and want to appropriately convey this, without going to what we believe would be an unjustified extreme of saying there is no evidence. 

Reviewer #2 (Public Review):

We thank the reviewer for the comprehensive summary and for highlighting both the technical achievement and biological relevance of our study. We greatly appreciate the thoughtful suggestions that have helped us refine our presentation and terminology.

(1) Some titles contain strong terms that do not fully match the conclusions of the corresponding sections.

(1a) Article title “Mouse germline cysts contain a fusome-like structure that mediates oocyte development”

We will change the statement to: “Mouse germline cysts contain a fusome that supports germline cyst polarity and rejuvenation.”

(1b) Result title “Visham overlaps centrosomes and moves on microtubules” We acknowledge that “moves” implies dynamics. We will include additional supplementary images showing small vesicular components of the mouse fusome on spindle-derived microtubule tracks.

(1c) Result title “Visham associates with Golgi genes involved in UPR beginning at the onset of cyst formation”

We will revise this title to: “The mouse fusome associates with the UPR regulatory protein Xbp1 beginning at the onset of cyst formation” to reflect the specific UPR protein that was immunolocalized. 

(1d) Result title “Visham participates in organelle rejuvenation during meiosis”

We will revise this to: “The mouse fusome persists during organelle rejuvenation in meiosis.”

(2) The authors aim to demonstrate that Visham is a fusome-like structure. I would suggest simply referring to it as a "fusome-like structure" rather than introducing a new term, which may confuse readers and does not necessarily help the authors' goal of showing the conservation of this structure in Drosophila and Xenopus germ cells. Interestingly, in a preprint from the same laboratory describing a similar structure in Xenopus germ cells, the authors refer to it as a "fusome-like structure (FLS)" (Davidian and Spradling, BioRxiv, 2025).

We appreciate the reviewer’s insightful comment. To maintain conceptual clarity and align with existing literature, we will refer to the structure as the mouse fusome throughout the manuscript, avoiding introduction of a new term.

Reviewer #3 (Public Review):

We thank the reviewer for emphasizing the importance of our study and for providing constructive feedback that will help us clarify and strengthen our conclusions.

(1) Line 86 - the heading for this section is "PGCs contain a Golgi-rich structure known as the EMA granule" 

We agree that the enrichment of Golgi within the EMA PGCs was not shown until the next section. We will revise this heading to:

“PGCs contain an asymmetric EMA granule.”

(2)  Line 105-106, how do we know if what's seen by EM corresponds to the EMA1 granule?

We will clarify that this identification is based on co-localization with Golgi markers (GM130 and GS28) and response to Brefeldin A treatment, which will be included as supplementary data. These findings support that the mouse fusome is Golgi-derived and can therefore be visualized by EM. The Golgi regions in E13.5 cyst cells move close together and associate with ring canals as visualized by EM (Figure 1E), the same as the mouse fusomes identified by EMA.

(3) Line 106-107-states "Visham co-stained with the Golgi protein Gm130 and the recycling endosomal protein Rab11a1". This is not convincing as there is only one example of each image, and both appear to be distorted.

Space is at a premium in these figures, but we have no limitation on data documenting this absolutely clear co-localization. We will replace the existing images with high-resolution, non-compressed versions for the final figures to clearly illustrate the co-staining patterns for GM130 and Rab11a1.

(4) Line 132-133---while visham formation is disrupted when microtubules are disrupted, I am not convinced that visham moves on microtubules as stated in the heading of this section.

We will include additional supplementary data showing small mouse fusome vesicles aligned along microtubules.

(5) Line 156 - the heading for this section states that Visham associates with polarity and microtubule genes, including pard3, but only evidence for pard3 is presented.

We agree and will revise the heading to: “Mouse fusome associates with the polarity protein Pard3.” We are adding data showing association of small fusome vesicles on microtubules.  

(6)  Lines 196-210 - it's strange to say that UPR genes depend on DAZ, as they are upregulated in the mutants. I think there are important observations here, but it's unclear what is being concluded.

UPR genes are not upregulated in DAZ in the sense we have never documented them increasing. We show that UPR genes during this time behave like pleuripotency genes and normally decline, but in DAZ mutants their decline is slowed.  We will rephrase the paragraph to clarify that Dazl mutation partially decouples developmental processes that are normally linked, which alters UPR gene expression relative to cyst development.

(7) Line 257-259-wave 1 and 2 follicles need to be explained in the introduction, and how these fits with the observations here clarified.

Follicle waves are too small a focus of the current study to explain in the introduction, but we will request readers to refer to the cited relevant literature (Yin and Spradling, 2025) for further details.

We sincerely thank all reviewers for their insightful and constructive feedback. We believe that the planned revisions—particularly the refined terminology, improved image quality, clarified statistics, and restructured abstract—will substantially strengthen the manuscript and enhance clarity for readers.

eLife Assessment

The authors combine experiments and mathematical modeling to determine how the infectivity of human cytomegalovirus scales with the viral concentration in the inoculum, i.e., considering the multiplicity of infection (MOI). They propose and test different model assumptions to explain a mechanism termed "apparent cooperativity" of virions based on an observed super-linear increase in the number of infected cells with increasing inocula. The authors present a solid study showing valuable findings for virologists and quantitative scientists working on the analysis and interpretation of viral infection dynamics. Some of the presented aspects would benefit from additional clarification.

Reviewer #1 (Public review):

Summary:

In this paper, the authors conduct both experiments and modeling of human cytomegalovirus (HCMV) infection in vitro to study how the infectivity of the virus (measured by cell infection) scales with the viral concentration in the inoculum. A naïve thought would be that this is linear in the sense that doubling the virus concentration (and thus the total virus) in the inoculum would lead to doubling the fraction of infected cells. However, the authors show convincingly that this is not the case for HCMV, using multiple strains, two different target cells, and repeated experiments. In fact, they find that for some regimens (inoculum concentration), infected cells increase faster than the concentration of the inoculum, which they term "apparent cooperativity". The authors then provided possible explanations for this phenomenon and constructed mathematical models and simulations to implement these explanations. They show that these ideas do help explain the cooperativity, but they can't be conclusive as to what the correct explanation is. In any case, this advances our knowledge of the system, and it is very important when quantitative experiments involving MOI are performed.

Strengths:

Careful experiments using state-of-the-art methodologies and advancing multiple competing models to explain the data.

Weaknesses:

There are minor weaknesses in explaining the implementation of the model. However, some specific assumptions, which to this reviewer were unclear, could have a substantial impact on the results. For example, whether cell infection is independent or not. This is expanded below.

Suggestions to clarify the study:

(1) Mathematically, it is clear what "increase linearly" or "increase faster than linearly" (e.g., line 94) means. However, it may be confusing for some readers to then look at plots such as in Figure 2, which appear linear (but on the log-log scale) and about which the authors also say (line 326) "data best matching the linear relationship on a log-log scale".

(2) One of the main issues that is unclear to me is whether the authors assume that cell infection is independent of other cells. This could be a very important issue affecting their results, both when analyzing the experimental data and running the simulations. One possible outcome of infection could be the generation of innate mediators that could protect (alter the resistance) of nearby cells. I can imagine two opposite results of this: i) one possibility is that resistance would lead to lower infection frequencies and this would result in apparent sub-linear infection (contrary to the observations); or ii) inoculums with more virus lead to faster infection, which doesn't allow enough time for the "resistance" (innate effect) to spread (potentially leading to results similar to the observations, supra-linear infection).

(3) Another unclear aspect of cell infection is whether each cell only has one chance to be infected or multiple chances, i.e., do the authors run the simulation once over all the cells or more times?

(4) On the other hand, the authors address the complementary issue of the virus acting independently or not, with their clumping model (which includes nice experimental measurements). However, it was unclear to me what the assumption of the simulation is in this case. In the case of infection by a clump of virus or "viral compensation", when infection is successful (the cell becomes infected), how many viruses "disappear" and what happens to the rest? For example, one of the viruses of the clump is removed by infection, but the others are free to participate in another clump, or they also disappear. The only thing I found about this is the caption of Figure S10, and it seems to indicate that only the infected virus is removed. However, a typical assumption, I think, is that viruses aggregate to improve infection, but then the whole aggregate participates in infection of a single cell, and those viruses in the clump can't participate in other infections. Viral cooperativity with higher inocula in this case would be, perhaps, the result of larger numbers of clumps for higher inocula. This seems in agreement with Figure S8, but was a little unclear in the interpretation provided.

(5) In algorithm 1, how does P_i, as defined, relate to equation 1?

(6) In line 228, and several other places (e.g., caption of Table S2), the authors refer to the probability of a single genome infecting a cell p(1)=exp(-lambda), but shouldn't it be p(1)=1-exp(-lambda) according to equation 1?

(7) In line 304, the accrued damage hypothesis is defined, but it is stated as a triggering of an antiviral response; one would assume that exposure to a virion should increase the resistance to infection. Otherwise, the authors are saying that evolution has come up with intracellular viral resistance mechanisms that are detrimental to the cell. As I mentioned above, this could also be a mechanism for non-independent cell infection. For example, infected cells signal to neighboring cells to "become resistance" to infection. This would also provide a mechanism for saturation at high levels.

(8) In Figure 3, and likely other places, t-tests are used for comparisons, but with only an n=5 (experiments). Many would prefer a non-parametric test.

Reviewer #2 (Public review):

In their article, Peterson et al. wanted to show to what extent the classical "single hit" model of virion infection, where one virion is required to infect a cell, does not match empirical observations based on human cytomegalovirus in vitro infection model, and how this would have practical impacts in experimental protocols.

They first used a very simple experimental assay, where they infected cells with serially diluted virions and measured the proportion of infected cells with flow cytometry. From this, they could elegantly show how the proportion of infected cells differed from a "single hit" model, which they simulated using a simple mathematical model ("powerlaw model"), and better fit a model where virions need to cooperate to infect cells. They then explore which mechanism could explain this apparent cooperation:

(1) Stochasticity alone cannot explain the results, although I am unsure how generalizable the results are, because the mathematical model chosen cannot, by design, explain such observations only by stochasticity.

(2) Virion clumping seemed not to be enough either to generally explain such a pattern. For that, they first use a mathematical model showing that the apparent cooperation would be small. However, I am unsure how extreme the scenario of simulated virion clumping is. They then used dynamic light scattering to measure the distribution of the sizes of clumps. From these estimates, they show that virion clumps cannot reproduce the observed virion cooperation in serial dilution assays. However, the authors remain unprecise on how the uncertainty of these clumps' size distribution would impact the results, as most clumps have a size smaller than a single virion, leaving therefore a limited number of clumps truly containing virions.

The two models remain unidentifiable from each other but could explain the apparent virion cooperativity: either due to an increase in susceptibility of the cell each time a virion tries to infect it, or due to viral compensation, where lesser fit viruses are able to infect cells in co-infection with a better fit virion. Unfortunately, the authors here do not attempt to fit their mathematical model to the experimental data but only show that theoretical models and experimental data generate similar patterns regarding virion apparent cooperation.

Finally, the authors show that this virions cooperation could make the relationship between the estimated multiplicity of infection and viruses/cell deviate from the 1:1 relationship. Consequently, the dilution of a virion stock would lead to an even stronger decrease in infectivity, as more diluted virions can cooperate less for infection.

Overall, this work is very valuable as it raises the general question of how the estimate of infectivity can be biased if extrapolated from a single virus titer assay. The observation that HCMV virions often cooperate and that this cooperation varies between contexts seems robust. The putative biological explanations would require further exploration.

This topic is very well known in the case of segmented viruses and the semi-infectious particles, leading to the idea of studying "sociovirology", but to my knowledge, this is the first time that it was explored for a nonsegmented virus, and in the context of MOI estimation.

Reviewer #3 (Public review):

Summary:

The authors dilute fluorescent HCMV stocks in small steps (df ≈ 1.3-1.5) across 23 points, quantify infections by flow cytometry at 3 dpi, and fit a power-law model to estimate a cooperativity parameter n (n > 1 indicates apparent cooperativity). They compare fibroblasts vs epithelial cells and multiple strains/reporters, and explore alternative mechanisms (clumping, accrued damage, viral compensation) via analytical modeling and stochastic simulations. They discuss implications for titer/MOI estimation and suggest a method for detecting "apparent cooperativity," noting that for viruses showing this behavior, MOI estimation may be biased.

Strengths:

(1) High-resolution titration & rigor: The small-step dilution design (23 serial dilutions; tailored df) improves dose-response resolution beyond conventional 10× series.

(2) Clear quantitative signal: Multiple strain-cell pairs show n > 1, with appropriate model fitting and visualization of the linear regime on log-log axes.

(3) Mechanistic exploration: Side-by-side modeling of clumping vs accrued damage vs compensation frames testable hypotheses for cooperativity.

Weaknesses:

(1) Secondary infection control: The authors argue that 3 dpi largely avoids progeny-mediated secondary infection; this claim should be strengthened (e.g., entry inhibitors/control infections) or add sensitivity checks showing results are robust to a small secondary-infection contribution.

(2) Discriminating mechanisms: At present, simulations cannot distinguish between accrued damage and viral compensation. The authors should propose or add a decisive experiment (e.g., dual-color coinfection to quantify true coinfection rates versus "priming" without coinfection; timed sequential inocula) and outline expected signatures for each mechanism.

(3) Decline at high genomes/cell: Several datasets show a downturn at high input. Hypotheses should be provided (cytotoxicity, receptor depletion, and measurement ceiling) and any supportive controls.

(4) Include experimental data: In Figure 6, please include the experimentally measured titers (IU/mL), if available.

(5) MOI guidance: The practical guidance is important; please add a short "best-practice box" (how to determine titer at multiple genomes/cell and cell densities; when single-hit assumptions fail) for end-users.

Author response:

Reviewer #1 (Public review):

Summary:

In this paper, the authors conduct both experiments and modeling of human cytomegalovirus (HCMV) infection in vitro to study how the infectivity of the virus (measured by cell infection) scales with the viral concentration in the inoculum. A naïve thought would be that this is linear in the sense that doubling the virus concentration (and thus the total virus) in the inoculum would lead to doubling the fraction of infected cells. However, the authors show convincingly that this is not the case for HCMV, using multiple strains, two different target cells, and repeated experiments. In fact, they find that for some regimens (inoculum concentration), infected cells increase faster than the concentration of the inoculum, which they term "apparent cooperativity". The authors then provided possible explanations for this phenomenon and constructed mathematical models and simulations to implement these explanations. They show that these ideas do help explain the cooperativity, but they can't be conclusive as to what the correct explanation is. In any case, this advances our knowledge of the system, and it is very important when quantitative experiments involving MOI are performed.

Strengths:

Careful experiments using state-of-the-art methodologies and advancing multiple competing models to explain the data.

Weaknesses:

There are minor weaknesses in explaining the implementation of the model. However, some specific assumptions, which to this reviewer were unclear, could have a substantial impact on the results. For example, whether cell infection is independent or not. This is expanded below.

Suggestions to clarify the study:

(1) Mathematically, it is clear what "increase linearly" or "increase faster than linearly" (e.g., line 94) means. However, it may be confusing for some readers to then look at plots such as in Figure 2, which appear linear (but on the log-log scale) and about which the authors also say (line 326) "data best matching the linear relationship on a log-log scale". 

This is a good point. In our revision, we will include a clarification to indicate that linear on the log-log scale relationship does not imply linear relationship on the linear-linear scale.

(2) One of the main issues that is unclear to me is whether the authors assume that cell infection is independent of other cells. This could be a very important issue affecting their results, both when analyzing the experimental data and running the simulations. One possible outcome of infection could be the generation of innate mediators that could protect (alter the resistance) of nearby cells. I can imagine two opposite results of this: i) one possibility is that resistance would lead to lower infection frequencies and this would result in apparent sub-linear infection (contrary to the observations); or ii) inoculums with more virus lead to faster infection, which doesn't allow enough time for the "resistance" (innate effect) to spread (potentially leading to results similar to the observations, supra-linear infection). 

In our models we assumed cells to be independent of each other (see also responses to other similar points). Because we measure infection in individual cells, assuming cells are independent is a reasonable first approximation. However, the reviewer makes an excellent point that there may be some between-cell signaling happening in the culture that “alerts” or “conditions” cells to change their “resistance”. It is also possible that at higher genome/cell numbers, exposure of cells to virions or virion debris may change the state of cells in the culture, and more cells become “susceptible” to infection. This is a good point that we will list in Limitations subsection of Discussion; it is a good hypothesis to test in our future experiments.

(3) Another unclear aspect of cell infection is whether each cell only has one chance to be infected or multiple chances, i.e., do the authors run the simulation once over all the cells or more times? 

Each cell has only one chance to be infected. Algorithm 1 clearly states that; we will add an extra sentence in “Agent-based simulations” to indicate this point.

(4) On the other hand, the authors address the complementary issue of the virus acting independently or not, with their clumping model (which includes nice experimental measurements). However, it was unclear to me what the assumption of the simulation is in this case. In the case of infection by a clump of virus or "viral compensation", when infection is successful (the cell becomes infected), how many viruses "disappear" and what happens to the rest? For example, one of the viruses of the clump is removed by infection, but the others are free to participate in another clump, or they also disappear. The only thing I found about this is the caption of Figure S10, and it seems to indicate that only the infected virus is removed. However, a typical assumption, I think, is that viruses aggregate to improve infection, but then the whole aggregate participates in infection of a single cell, and those viruses in the clump can't participate in other infections. Viral cooperativity with higher inocula in this case would be, perhaps, the result of larger numbers of clumps for higher inocula. This seems in agreement with Figure S8, but was a little unclear in the interpretation provided. 

This is a good point. We did not remove the clump if one of the virions in the clump manages to infect a cell, and indeed, this could be the reason why in some simulations we observe apparent cooperativity when modeling viral clumping. This is something we will explore in our revision.

(5) In algorithm 1, how does P_i, as defined, relate to equation 1? 

These are unrelated because eqn.(1) is a phenomenological model that links infection per cell to genomes per cell. P_i in algorithm 1 is “physics-inspired” potential barrier.

(6) In line 228, and several other places (e.g., caption of Table S2), the authors refer to the probability of a single genome infecting a cell p(1)=exp(-lambda), but shouldn't it be p(1)=1-exp(-lambda) according to equation 1?

Indeed, it was a typo, p(1)=1-exp(-lambda) per eqn 1. Thank you, it will be corrected in the revised paper.

(7) In line 304, the accrued damage hypothesis is defined, but it is stated as a triggering of an antiviral response; one would assume that exposure to a virion should increase the resistance to infection. Otherwise, the authors are saying that evolution has come up with intracellular viral resistance mechanisms that are detrimental to the cell. As I mentioned above, this could also be a mechanism for non-independent cell infection. For example, infected cells signal to neighboring cells to "become resistance" to infection. This would also provide a mechanism for saturation at high levels. 

We do not know how exposure of a cell to one virion would change its “antiviral state”, i.e., to become more or less resistant to the next infection. If a cell becomes more resistant, there is no possibility to observe apparent cooperativity in infection of cells, so this hypothesis cannot explain our observations with n>1. Whether this mechanism plays a role in saturation of cell infection rate at lower than 1 value when genome/cell is large is unclear but is a possibility. We will add this point to Discussion in revision.

(8) In Figure 3, and likely other places, t-tests are used for comparisons, but with only an n=5 (experiments). Many would prefer a non-parametric test. 

We repeated the analyses in Fig 3 with Mann-Whitney test, results were the same, so we would like to keep results from the t-test in the paper.

Reviewer #2 (Public review):

In their article, Peterson et al. wanted to show to what extent the classical "single hit" model of virion infection, where one virion is required to infect a cell, does not match empirical observations based on human cytomegalovirus in vitro infection model, and how this would have practical impacts in experimental protocols.

They first used a very simple experimental assay, where they infected cells with serially diluted virions and measured the proportion of infected cells with flow cytometry. From this, they could elegantly show how the proportion of infected cells differed from a "single hit" model, which they simulated using a simple mathematical model ("powerlaw model"), and better fit a model where virions need to cooperate to infect cells. They then explore which mechanism could explain this apparent cooperation:

(1) Stochasticity alone cannot explain the results, although I am unsure how generalizable the results are, because the mathematical model chosen cannot, by design, explain such observations only by stochasticity. 

Our null model simulations are not just about stochasticity; they also include variability in virion infectivity and cell resistance to infection. We agree that simulations cannot truly prove that such variability cannot result in apparent cooperativity; however, we also provide a mathematical proof that increase in frequency of infected cells should be linear with virion concentration at small genome/cell numbers.

(2) Virion clumping seemed not to be enough either to generally explain such a pattern. For that, they first use a mathematical model showing that the apparent cooperation would be small. However, I am unsure how extreme the scenario of simulated virion clumping is. They then used dynamic light scattering to measure the distribution of the sizes of clumps. From these estimates, they show that virion clumps cannot reproduce the observed virion cooperation in serial dilution assays. However, the authors remain unprecise on how the uncertainty of these clumps' size distribution would impact the results, as most clumps have a size smaller than a single virion, leaving therefore a limited number of clumps truly containing virions. 

As we stated in the paper, clumping may explain apparent cooperativity in simulations depending on how stock dilution impacts distribution of virions/clump. This could be explored further, however, better experimental measurements of virions/clump would be highly informative (but we do not have resources to do these experiments at present). Our point is that the degree of apparent cooperativity is dependent on the target cell used (n is smaller on epithelial cells than on fibroblasts) that is difficult to explain by clumping which is a virion property. Per comment by reviewer 1, we will do some more analyses of the clumping model to investigate importance of clump removal per successful infection on the detected degree of apparent cooperativity.

The two models remain unidentifiable from each other but could explain the apparent virion cooperativity: either due to an increase in susceptibility of the cell each time a virion tries to infect it, or due to viral compensation, where lesser fit viruses are able to infect cells in co-infection with a better fit virion. Unfortunately, the authors here do not attempt to fit their mathematical model to the experimental data but only show that theoretical models and experimental data generate similar patterns regarding virion apparent cooperation. 

In the revision we will provide examples of simulations that “match” experimental data with a relatively high degree of apparent cooperativity; we have done those before but excluded them from the current version since they are a bit messy. Fitting simulations to data may be an overkill.

Finally, the authors show that this virions cooperation could make the relationship between the estimated multiplicity of infection and viruses/cell deviate from the 1:1 relationship. Consequently, the dilution of a virion stock would lead to an even stronger decrease in infectivity, as more diluted virions can cooperate less for infection.

Overall, this work is very valuable as it raises the general question of how the estimate of infectivity can be biased if extrapolated from a single virus titer assay. The observation that HCMV virions often cooperate and that this cooperation varies between contexts seems robust. The putative biological explanations would require further exploration.

This topic is very well known in the case of segmented viruses and the semi-infectious particles, leading to the idea of studying "sociovirology", but to my knowledge, this is the first time that it was explored for a nonsegmented virus, and in the context of MOI estimation. 

Thank you.

Reviewer #3 (Public review): 

Summary:

The authors dilute fluorescent HCMV stocks in small steps (df ≈ 1.3-1.5) across 23 points, quantify infections by flow cytometry at 3 dpi, and fit a power-law model to estimate a cooperativity parameter n (n > 1 indicates apparent cooperativity). They compare fibroblasts vs epithelial cells and multiple strains/reporters, and explore alternative mechanisms (clumping, accrued damage, viral compensation) via analytical modeling and stochastic simulations. They discuss implications for titer/MOI estimation and suggest a method for detecting "apparent cooperativity," noting that for viruses showing this behavior, MOI estimation may be biased.

Strengths:

(1) High-resolution titration & rigor: The small-step dilution design (23 serial dilutions; tailored df) improves dose-response resolution beyond conventional 10× series.

(2) Clear quantitative signal: Multiple strain-cell pairs show n > 1, with appropriate model fitting and visualization of the linear regime on log-log axes.

(3) Mechanistic exploration: Side-by-side modeling of clumping vs accrued damage vs compensation frames testable hypotheses for cooperativity. 

Thank you.

Weaknesses:

(1) Secondary infection control: The authors argue that 3 dpi largely avoids progeny-mediated secondary infection; this claim should be strengthened (e.g., entry inhibitors/control infections) or add sensitivity checks showing results are robust to a small secondary-infection contribution. 

This is an important point. We do believe that the current knowledge about HCMV virion production time – it takes 3-4 days to make virions per multiple papers (see Fig 7 in Vonka and Benyesh-Melnick JB 1966; Fig 3B in Stanton et al JCI 2010; and Fig 1A in Li et al. PNAS 2015) – is sufficient to justify our experimental design but we do agree that an additional control to block novel infections with would be useful. We had previously performed experiments with a HCMV TB-gL-KO that cannot make infectious virions (but the stock virions can be made from complemented target cells). We will investigate if our titration experiments with this virus strain have sufficient resolution to detect apparent cooperativity. However, at present we do not have the resources to perform novel experiments.  

(2) Discriminating mechanisms: At present, simulations cannot distinguish between accrued damage and viral compensation. The authors should propose or add a decisive experiment (e.g., dual-color coinfection to quantify true coinfection rates versus "priming" without coinfection; timed sequential inocula) and outline expected signatures for each mechanism. 

Excellent suggestion. Because infection of a cell is a result of the joint viral infectivity and cell resistance, it may be hard to discriminate between these alternatives unless we specify them as particular molecular mechanisms. But we will try our best and list potential future experiments in the revised version of the paper.

(3) Decline at high genomes/cell: Several datasets show a downturn at high input. Hypotheses should be provided (cytotoxicity, receptor depletion, and measurement ceiling) and any supportive controls. 

Another good point. We do not have a good explanation, but we do not believe this is because of saturation of available target cells.  It seemed to only happen (or was most pronounced) with the ME stocks, which are typically lower in titer and so the higher MOI were nearly undiluted stock. It may be the effect of the conditioned medium.  Or perhaps there are non-infectious particles like dense bodies (enveloped particles that lack a capsid and genome) and non-infectious, enveloped particles (NIEPs) that compete for receptors or otherwise damage cells and these don’t get diluted out at the higher doses.  We plan to include these points in Discussion of the revised version of the paper.

(4) Include experimental data: In Figure 6, please include the experimentally measured titers (IU/mL), if available. 

This is a model-simulated scenario, and as such, there is no measured titers.

(5) MOI guidance: The practical guidance is important; please add a short "best-practice box" (how to determine titer at multiple genomes/cell and cell densities; when single-hit assumptions fail) for end-users. 

Good suggestion. We will include best-practice box using guidelines developed in Ryckman lab over the years in the revised version of the paper.

Overall note to all reviews: We have deposited our codes and the data on github; yet, none of the reviewers commented on it.

eLife Assessment

This manuscript reports on the application of ribosome profiling (EZRA-seq and eRF1-seq) combined with massively parallel reporter assays to identify and characterize a GA-rich element associated with ribosome pausing during translation termination. While the development of eRF1-seq is useful and the identification of GA-rich elements upstream of stop codons is convincing, the level of support for other claims is inadequate. Specifically, the evidence that GA-rich sequences upstream of stop codons can base-pair with the 3′ end of 18S rRNA to prolong ribosome dwell time, and the evidence that Rps26 interferes with this interaction to regulate translation termination, are not adequate.

Reviewer #1 (Public review):

Summary:

The authors use high-resolution ribosome profiling (Ezra-seq) and eRF1 pulldown-based ribosome profiling (eRF1-seq) developed in their lab to identify a GA rich sequence motif located upstream of the stop codon responsible for translation termination pausing. They then perform a massively parallel assay with randomly generated sequences to further characterize this motif. Using mouse tissues, they show that termination pausing signatures can be tissue-specific. They use a series of published ribosome structures and 18S rRNA mutants, and eS26 knockdown experiments to propose that the GA rich sequence interacts with the 3′-end of the 18S rRNA.

Strengths:

(1) Robust ribosome profiling data and clear analyses clarify the subtle behavior of terminating ribosomes near the stop codon.

(2) Novel termination or "false termination" sites revealed by eRF1-seq in the 5′-UTR, 3′-UTR, and CDS highlight a previously underappreciated facet of translation dynamics.

Weakness:

(1) Modest effects seen in ABCE1 knockdown do not seem to add up to the level of regulation. The authors state "ABCE1 regulates terminating ribosomes independent of the sequence context" on pg 9, and "ABCE1 modulates termination pausing independent of the mRNA sequence context" in the figure caption for Figure S4. Given the modest effect of the knockdown, such phrasing is most likely not supported. Further clarification of "ABCE1 plays a generic role in translation termination" is necessary.

(2) The authors propose that the GA rich sequence element upstream of the stop codon on the mRNA could potentially base pair with the 3′-end of the 18S rRNA. In the PDBs the authors reference in their paper and also in 3JAG, 3JAH, 3JAI (structures of terminating ribosomes with the stop codon in the A-site and eRF1), the mRNA exiting the ribosome and the 3′-end of the 18S rRNA are about 25-30 A apart. In addition, a segment of eS26 is wedged in between these two RNA segments. This reviewer noted this arrangement in a random sampling of 5 other PDBs of mammalian and human ribosome 80S structures. How do the authors anticipate the base pairing they have proposed to occur in light of these steric hindrances? RpsS26 is known to be released by Tsr2 in yeast during very specific stresses. Is it their expectation that termination pausing in human/mammalian cells happens during stressful conditions only?

(3) The authors say, "It is thus likely that mRNA undergoes post-decoding scanning by 18S rRNA." (pg. 10). It is unclear what the authors mean by "scanning." Do they mean that the mRNA gets scanned in a manner similar to scanning during initiation? There is no evidence presented to support that particular conclusion.

(4) Role of termination pausing in the testis is highly speculative. The authors state: "It is thus conceivable that the wide range of ribosome density at stop codons in testis facilitates functional division of ribosome occupancy beyond the coding region." It is unclear what type of functional division they are referring to.

Reviewer #2 (Public review):

Summary:

This paper presents results interpreted to indicate that sequences upstream of stop codons capable of base-pairing with the 3' end of 18S rRNA prolong the dwell time of 80S ribosomes at stop codons in a manner impeded by Rps26 in the 40S subunit exit channel, which leads to the proper completion of termination and ribosome recycling and prevents spurious translation of 3'UTR sequences by one or more unconventional mechanisms.

Strengths:

The standard 80S and selective eRF1 80S ribosome profiling data obtained using EZRA-Seq are of high quality, allowing the authors to detect an enrichment for purine-rich sequences upstream of stop codons at sites where termination is relatively slow and ribosomal complexes are paused with eRF1 still engaged in the A site.

Weaknesses:

There are many weaknesses in the experimental design, interpretation of results, and description of assay design and assumptions, the data obtained, and the interpretation of results, all of which detract from the scientific quality and significance of this work. In fact, a large proportion of paragraphs in the text and figure panels present some difficulty either in understanding how the experiment or data analysis was conducted or what the authors wish to conclude from the results, or that stem from an overinterpretation of findings or failure to consider other equally likely explanations.

Reviewer #3 (Public review):

Summary:

This study from Jia et al carried out a variety of analyses of terminating ribosomes, including the development of eRF1-seq to map termination sites, identification of a GA-rich motif that promotes ribosome pausing, characterization of tissue-specific termination dynamics, and elucidation of the regulatory roles of 18S rRNA and RPS26. Overall, the study is thoughtfully designed, and its biological conclusions are well supported by complementary experiments. The tools and datasets generated provide valuable resources for researchers investigating the mechanisms of RNA translation.

Strengths:

(1) The study introduces eRF1-seq, a novel approach for mapping translation termination sites, providing a methodological advance for studying ribosome termination.

(2) Through integrative bioinformatic analyses and complementary MPRA experiments, the authors demonstrate that GA-rich motifs promote ribosome pausing at termination sites and reveal possible regulatory roles of 18S rRNA in this process.

(3) The study characterizes tissue-specific ribosome termination dynamics, showing that the testis exhibits stronger ribosome pausing at stop codons compared to other tissues. Follow-up experiments suggest that RPS26 may contribute to this tissue specificity.

Weaknesses:

The biological significance of ribosome pausing regulation at translation termination sites or of translational readthrough, for example, across different tissue types, remains unclear. Nevertheless, this question lies beyond the primary scope of the current study.

Reviewer #4 (Public review):

Summary:

This manuscript by Qian and colleagues utilizes ribosome profiling, and reporter assays to dissect translation termination. Unfortunately, the data do not support the conclusions of the paper, controls are missing and several assays are not well validated and do not reproduce previous findings from others.

Specific comments:

• Translation termination has been studied in several organisms including mammalian cells and yeast. In those cases what is analyzed is not the peak height at the stop codon, but rather the difference in the ribosome density before and after the stop. Thus, analyzing peak height is not validated. I understand that this is relevant only for the ribosome profiling experiments (and Ezra-seq) not the RF1 profiling. But much of the data was acquired that way.

• Moreover, the data do not reproduce previous findings and no effort is made to connect them to previous data. Previous data has shown that stop codon efficacy varies. This is not reproduced (S1C). Similarly, an effect from the +1 residue is not reproduced. The data isn't even stratified by different stop codons as previous work has shown that different surrounding residues have different effects in the context of different stop codons. Thus, none of the sequencing data is validated or trusted and does not reproduce previous findings.

• The GA-rich sequence identified by Ezra-Seq and RF1 seq is not the same and it differs from previous sequences (Wangen &Green).

• The authors claim that the majority of Rf1 peaks is at stop codons, but that is not true. It is only about 30% of the peaks. Also, not all mRNAs have peaks at the stop codons. That is at best problematic. Finally, there are mRNAs that are known to "suffer" from NMD, what do these look like in the Ezra-Seq and RF1-Seq? How about mRNAs that have programmed frameshifts? This raises questions on the validity of the eRF1 data.

• Figure 4: First, instead of M/P ratio, one should analyze M/M+P, to normalize out differences in the loading and effects from collisions, which are guaranteed to occur here, but not considered or analyzed. Second, the data are analyzed as if what matters are codons in the P and E site (and beyond, where there are definitely NOT recognized codons). While there is evidence for some interactions, one would think that an additional analysis based on sequence would be helpful. Also, the supplemental data indicates that very rarely are there reciprocal changes (as should be the case), and as seen for stop codons.

• Regarding the HiBit reporter assay: The two sequecnes clearly have effects on translation without considering stop codon context (Figure 4C), which need to be taken into account. Also, the effect from the sequences varies in the context of the assay in 4C and 4D (2-fold vs .5 fold), further questioning the assay. Moreover, the authors claim that re-initiation cannot account for Hibit levels, but that is clearly incorrect. The western in Figure 4E does not reproduce the data in 4D. While Hibit goes up (as in 4D, the putative GFP-fusion goes down. Finally, while the second reading frame should be more efficient is not explained and further argues for an artifact. Previous work (and work herein) suggests that read-through occurs equally in each reading frame. No controls for these assays are presented: e.g. stimulation by antibiotics, ABCE1 depletion, etc.

• Figure 5 has similar problems. I don't understand how the Figure in 5A is made, but when you overlay the cited structures on Rps26, the molecules are identical. I guess the authors used some fantasy to build non-existing sequences differently into the structure. There is no basis for that. In panel C and the same in Figure 7, the number of analyzed mRNAs varies. This could influence the outcome and the EXACT same set of mRNAs should be analyzed. But the main problem here is that the authors need to analyze readthrough and not peak height as detailed above. Essential controls are missing that show what fraction of the 18S rRNA is mutated. Previous work has shown that 2 nt truncated 18S rRNA is actively degraded. It is hard to believe how 15% of altered ribosomes can abolish 100% of the effect from the C-rich sequences. Important validation is missing: the authors should analyze rRNA sequences in their ribo-seq dataset to demonstrate that they have the mutated rRNAs, and that these enrich and de-enrich as predicted.

• In Figure 5-7 the authors develop a model that the sequence selectivity arises from base pairing between 18S rRNA and the mRNA. If so, then they should really stratify the data by number of WC pairs that can be formed. And only WC pairs, as GU pairs have a totally different geometry that will likely be discriminated against in this context. Also, the mutation is in a part of the helix that has no effect (Figure S3G). Thus, the data within the manuscript are inconsistent.

• Figure 6 does not agree with published data (Li et al., Nature 2022). Previous work did not show testis-depletion of Rps26 in purified ribosomes. This is the critical difference as the authors here did not purify ribosomes. Also, another Rps is an essential control, even if purified ribosomes are used. The validity of this dataset is thus questionable . Depletion from polysomes is hard to believe, as overall there is less signal in the polysomes.

• Figure 7 has similar problems as figure 5. Different pools of mRNAs are analyzed; peak height is not validated. Overexpression of Rps26 is not shown, as only Myc is shown, not Rps26. Beyond that, increased occupancy in ribosomes needs to be shown for the effect to come from ribosomes. Given how sick the cells are it is most likely that all effects are secondary and arise from whatever else is going on in the overexpression or depletion of Rps26. No controls are presented to show specific effects from Rps26.

• The authors need to check Rli1/ABCE levels in their cells. Their data have features that are indicative of low ABCE1 levels. These include a very small effect from ABCE1 depletion. These could be responsible for some of the effects they observe.

Author response:

We thank the editor and reviewers for their thoughtful feedback. We agree with eLife’s overall assessment that, while profiling terminating ribosomes is informative in revealing termination dynamics, the underlying mechanisms require more evidence. Our revision will focus on three conceptual points.

(1) We will tone down the statement that putative mRNA:rRNA interaction contributes to sequence-specific termination pausing.

(2) We will clarify the potential role of Rps26 in regulating translation termination.

(3) We will expand the discussion of tissue-specific termination pausing.

Reviewer #1 (Public Review):

(1) We admit that the modest effects of ABCE1 were partly due to the incomplete ABCE1 knockdown in HEK293 cells. Since the elevated ribosome density occurred at all stop codons, we argue that the action of ABCE1 is likely independent of the sequence context. We will rephrase relevant statements in the revised manuscript.

(2) In terms of Rps26 structures, we agree the structural rearrangement in the absence of Rps26 is highly speculative. However, we do not believe the Rps26 stoichiometry is solely dependent on stress. We will clarify this important point in the revised manuscript.

(3) We apologize for the confusion about 18S rRNA “scanning” and will revise the sentence in the main text.

(4) We agree that functional significance of testis-specific termination dynamics is unclear. Since other reviewers raised similar concern, we will expand the discussion of tissue-specific termination pausing in the revised manuscript.

Reviewer #2 (Public Review):

We appreciate the Reviewer’s time and efforts in reviewing our manuscript. We are grateful for the insightful comments and many recommendations made by the reviewer to improve our manuscript. We feel that the reviewer may have some misunderstanding in terms of the sequence motif associated with the termination pausing, partly because of the lack of clarity in our original description of the results from MPRA and reporter assays. We will ensure that the reviewer’s points are fully addressed in the revised manuscript.

Reviewer #3 (Public Review):

We thank the reviewer’s positive comment on our manuscript. We agree that the tissue-specific termination differences were poorly described in the main text. Notably, other reviewers raised similar concerns. We will expand the relevant discussion in the revised manuscript, outlining this as a limitation and a future direction.

Reviewer #4 (Public Review):

We believe the reviewer mixed xthe public view with recommendation comments. The reviewer appears to be preoccupied by previous studies and questioned some inconsistency in our results. With the development of new technology such as eRF1-seq, we are encouraged to present “new” and “different” findings. All other reviewers appreciate the development of eRF1-seq to profile terminating ribosomes. In fact, we do not believe our data is fundamentally different from the established principles. Rather, our data provides new perspectives to further our understanding of ribosome dynamics at stop codons. We thank the reviewer for understanding.

The reviewer is quite confused by our sequencing analysis based on peak height, or read density, which is commonly used to infer ribosome dynamics such as pausing. Regarding the sequencing analysis and reporter assays in cells expressing 18S mutant (Figure 5) and Rps26 (Figure 7), we feel that the reviewer has some misunderstanding. In the revised manuscript, we will do our best to clarify those relevant issues. Finally, the reviewer’s comment on base pairing is well-received and we will thoroughly revise the main text and discussion in the revised manuscript.

eLife Assessment

The authors investigated the epigenetic mechanisms regulating the differentiation of circulating monocytes that infiltrate the CNS and adopt microglia-like characteristics. The work is useful to the field, as the contribution of circulating myeloid cell-derived microglia remains controversial. However, the evidence presented is inadequate as the analyses are based on a very limited set of genes, which does not sufficiently support the authors' central claims.

Reviewer #1 (Public review):

Microglia are mononuclear phagocytes in the CNS and play essential roles in physiology and pathology. In some conditions, circulating monocytes may infiltrate in the CNS and differentiated into microglia or microglia-like cells. However, the specific mechanism is large unknown. In this study, the authors explored the epigenetic regulation of this process. The quality of this study will be significantly improved if a few questions are addressed.

(1) The capacity of circulating myeloid cell-derived microglia are controversial. In this study, the authors utilized CX3CR1-GFP/CCR2-DsRed (hetero) mice as a lineage tracing line. However, this animal line is not an appropriate approach for this purpose. For example, when the CX3CR1-GFP/CCR2-DsRed as the undifferentiated donor cell, they are GFP+ and DsRed+. When the cell fate has been changed to microglia, they will change into GFP+ and DsRed- cells. However, this process is mediated with busulfan and artificially introduced bone marrow cells in the circulating cell, which is not existed in physiological and pathological conditions. These artifacts will potentially bring in artifacts and confound the conclusion, as the classical wrong text book knowledge of the bone marrow derived microglia theory and subsequently corrected by Fabio Rossi lab1,2. This is the most risk for drawing this conclusion. The top evidence is from the parabiosis animal model. Therefore, A parabiosis study before making this conclusion, combining a CX3CR1-GFP (hetero) mouse with a WT mouse without busulfan conditioning and looking at whether there are GFP+ microglia in the GFP- WT mouse brain. If there are no GFP+ microglia, the author should clarify this is not a physiological or pathological condition, but a defined artificial host condition, as previously study did3.

(2) In some conditions, peripheral myeloid cells can infiltrate and replace the brain microglia4,5. Discuss it would be helpful to better understand the mechanism of microglia replacement.

References:

(1) Ajami, B., Bennett, J.L., Krieger, C., Tetzlaff, W., and Rossi, F.M. (2007). Local self-renewal can sustain CNS microglia maintenance and function throughout adult life. Nature neuroscience 10, 1538-1543. 10.1038/nn2014.

(2) Ajami, B., Bennett, J.L., Krieger, C., McNagny, K.M., and Rossi, F.M.V. (2011). Infiltrating monocytes trigger EAE progression, but do not contribute to the resident microglia pool. Nature neuroscience 14, 1142-1149. http://www.nature.com/neuro/journal/v14/n9/abs/nn.2887.html#supplementary-information.

(3) Mildner, A., Schmidt, H., Nitsche, M., Merkler, D., Hanisch, U.K., Mack, M., Heikenwalder, M., Bruck, W., Priller, J., and Prinz, M. (2007). Microglia in the adult brain arise from Ly-6ChiCCR2+ monocytes only under defined host conditions. Nature neuroscience 10, 1544-1553. 10.1038/nn2015.